Experimental Landscape Ecology (Landscape Series, 29) [1st ed. 2022] 9783030951887, 9783030951894, 303095188X

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Landscape Series

Yolanda F. Wiersma

Experimental Landscape Ecology

Landscape Series Volume 29

Series Editors Christine Fürst, Martin Luther University Halle-Wittenberg, Halle (Saale), Sachsen-Anhalt, Germany Cristian Echeverria, Universidad de Concepción, Concepción, Chile Henry N. N. Bulley, BMCC, City University of New York, New York, NY, USA Editorial Board Members Buyanbaatar Avirmed, School of Agroecology, Mongolian University of Life Sciences, Ulaanbaatar, Mongolia Yazidhi Bamutaze, Dept of Geo Geo-Info & Climatic Sci, Makerere University, Kampala, Uganda Bolormaa Batsuuri, National University of Mongolia, Ulaanbaatar, Mongolia Mahamadou Belem, Nazi Boni University, Bobo Dioulasso, Burkina Faso Emiru Birhane, Dept. Land Resources Management, Mekelle University, London, UK Danilo Boscolo, FFCLRP, Departamento de Biologia, Universidade de Sao Paolo, Ribeirao Preto, São Paulo, Brazil Jiquan Chen, Center for Global Change & Earth Observa, Michigan State University, East Lansing, MI, USA Nicola Clerici, Department of Biology, Universidad del Rosario, Bogota, Colombia Marc Deconchat, National Research Institute for Agriculture, Castanet, France Andrés Etter, Fac. de Estudios Ambientales y Rurales, Pontificia Universidad Javeriana, Bogotá DC, Colombia Pawan K. Joshi, School of Environmental Sciences, Jawaharlal Nehru University, New Delhi, India Alexander Khoroshev, Dept. Physical Geography & Landscape Sc., Lomonosov Moscow State University, Moscow, Russia Felix Kienast, Swiss Federal Institute for Forest, Snow and Landscape Research WSL, Birmensdorf, Switzerland Ramesh Krishnamurthy, Department Landscape Level Planning, Wildlife Institute of India, Chandrabani, Dehradun, Uttarakhand, India Quang Bao Le, International Center for Agricultural Research in the Dry Areas, Cairo, Egypt Yu-Pin Lin, Dept of Bioenvi Systems Engineering, National Taiwan University, Taipei, Taiwan

Benjamin Kofi Nyarko, Dept of Geography & Regional Planning, University of Cape Coast, Cape Coast, Ghana Henrique Pereira, German Centre for Integrative Biodiversity Research (iDiv), Martin Luther University Halle-Wittenberg, Leipzig, Sachsen, Germany Alexander Prishchepov, Dept of Geosci & Natural Resource Mgmt, University of Copenhagen, Copenhagen, Denmark Robert M. Scheller, North Carolina State University, Raleigh, NC, USA Kalev Sepp, Inst. Agricultural & Environ. Sciences, Estonian University of Life Sciences, Tartu, Estonia Anton Shkaruba, Inst. of Agricultural & Environ Sciences, Estonian University of Life Sciences, Tartu, Estonia Janet Silbernagel Balster, Silvernail Studio for Geodesign, LLC, Black Earth, WI, USA Ileana Stupariu, Dept. Regional Geography and Environment, University of Bucharest, Bucharest, Romania Raymond Tutu, College of Humanities, Delaware State University, DOVER, DE, USA Teiji Watanabe, Fac of Environmental Earth Sci, A-301, Hokkaido University, Sapporo, Hokkaido, Japan Wei-Ning Xiang, University of North Carolina at Charlotte, Charlotte, NC, USA Qing Zhao, Institute of Applied Ecology, Chinese Academy of Sciences, Shenyang, China

Springer’s innovative Landscape Series is committed to publishing high quality manuscripts that approach the concept of landscape and land systems from a broad range of perspectives and disciplines. Encouraging contributions that are scientifically-grounded, solutions-oriented and introduce innovative concepts, the series attracts outstanding research from the natural and social sciences, and from the humanities and the arts. It also provides a leading forum for publications from interdisciplinary and transdisciplinary teams across the globe. The Landscape Series particularly welcomes contributions around several globally significant areas for landscape research, which are anyhow non-exclusive: • Climate and global change impacts on landscapes and ecosystems including mitigation and adaptation strategies • Human Dimensions of Global Change • Biodiversity and ecosystem processes linked to ecosystems, landscapes and regions • Biogeography • Ecosystem and landscape services including mapping, assessment and modelling • Land System Science • Regional ecology (including bioregional theory & application) • Human-Environment Interactions and Social-Ecological Systems & Frameworks (SESF) - including theories, practice and modelling Volumes in the series can be authored or edited works, cohesively connected around these and other related topics and tied to global or regional initiatives. Ultimately, the Series aims to facilitate the application of landscape research and land system science to practice in a changing world, and to advance the contributions of landscape theory and research and land system science to the broader scholarly community. More information about this series at https://link.springer.com/bookseries/6211

Yolanda F. Wiersma

Experimental Landscape Ecology

Yolanda F. Wiersma Department of Biology Memorial University St. John’s, NL, Canada

ISSN 1572-7742     ISSN 1875-1210 (electronic) Landscape Series ISBN 978-3-030-95188-7    ISBN 978-3-030-95189-4 (eBook) https://doi.org/10.1007/978-3-030-95189-4 © Springer Nature Switzerland AG 2022 This work is subject to copyright. All rights are reserved by the Publisher, whether the whole or part of the material is concerned, specifically the rights of translation, reprinting, reuse of illustrations, recitation, broadcasting, reproduction on microfilms or in any other physical way, and transmission or information storage and retrieval, electronic adaptation, computer software, or by similar or dissimilar methodology now known or hereafter developed. The use of general descriptive names, registered names, trademarks, service marks, etc. in this publication does not imply, even in the absence of a specific statement, that such names are exempt from the relevant protective laws and regulations and therefore free for general use. The publisher, the authors and the editors are safe to assume that the advice and information in this book are believed to be true and accurate at the date of publication. Neither the publisher nor the authors or the editors give a warranty, expressed or implied, with respect to the material contained herein or for any errors or omissions that may have been made. The publisher remains neutral with regard to jurisdictional claims in published maps and institutional affiliations. This Springer imprint is published by the registered company Springer Nature Switzerland AG The registered company address is: Gewerbestrasse 11, 6330 Cham, Switzerland

Acknowledgements

I was motivated to write this book by the experience of organizing a symposium on the topic of doing experiments in landscape ecology, which happened at the US-IALE meeting in Chicago in 2018. I thank the Chicago meeting organizers for the opportunity. At the end of the session, Darryl Jenerette suggested I write a book on the topic, so I took him up on the idea! I would like to offer my thanks to him and to all the presenters in that session, for initial inspiration. I owe a particular thanks to a cohort of graduate students who read very early drafts of many of these chapters during our fortnightly writing group. Thanks to Isabella (Bella) Richmond for organizing this group, and to Katherine Flores who took over as writing group coordinator after Bella graduated. I am grateful to my amazing lab group of Bella, Katherine, Hayley Paquette, Jennifer Rey-Goyenche, Ashley Locke, and Gabby Riefesel for reading the various parts of these chapters as they evolved. Your comments and feedback helped focus and refine many parts of this book. A special thank you to my colleague David Schneider for multiple helpful discussions and resources as I was writing Chap. 4, and to Anna Hargreaves who generously shared her database of “micro-landscape” papers, which helped immensely with Chaps. 8 and 11. I was able to improve substantially each of the individual chapters based on peer review and feedback. I thank the following (in alphabetical order) for their time and energy in looking at different parts of the book: Olivia Daniel, Rob Ewers, Ross Gray, Jeff Hollister, Darryl Jenerette, Joss Lyons-White, Amanda Martin, Shannon McCauley, Emily Minor, Simon Pittman, Dave Schneider, Thomas Smith, Terhi Riutta, Sarab Sethi, Dean Urban, Kathleen Vigness Raposa, Dave Wilson, and Kim With. A major thank you to Jiquan Chen for a comprehensive review of the entire manuscript (twice!). Any remaining errors and omissions are mine. I was fortunate to receive a half sabbatical from my home institution, Memorial University of Newfoundland & Labrador, during the fall semester of 2020, which facilitated finding the necessary time to write this book. The COVID-19 pandemic meant that I was not able to travel to an exotic destination on a writing retreat. However, I was able to write comfortably in my basement home office accompanied by my late pet rabbit (and foot warmer) Forest through the first half of the process, vii

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and with incentives for break walks provided by our new pet, the adopted husky Jack, during the second half of the process. I am immensely grateful for the love and support of my family. As a fellow academic, my husband John Sandlos understands well the writing process, and has always provided a listening ear and sounding board when needed. My teen boys, William and Xavier, are great sources of dinner conversation on a wide range of topics and are fantastic supporters of their “scientist mom.” I would not have been able to complete a project like this without “team Sandlos” on my side—thanks lads!

Contents

Part I Philosophy and Concepts of Experimentation 1 What Is Landscape Ecology? Why Do We Need a Book About Experimentation?������������������������������������������������������������    3 2 What Does It Mean to Do Experiments in Ecology? Historical Context and Current Approaches����������������������������������������   11 3 What Is It About Landscape Ecology That Makes Experimentation a Particular Challenge?�����������������������   23 4 Replication vs. Pseudoreplication: Are We Making Too Big a Deal of This?������������������������������������������������   35 5 Scale—We All Talk About It; What Do We Do With It?����������������������   55 Part II Approaches to Experimentation 6 Large-Scale Manipulative Experiments������������������������������������������������   73 7 Experimental Model Landscapes ����������������������������������������������������������   91 8 Mesocosms������������������������������������������������������������������������������������������������  105 9 Microcosms ����������������������������������������������������������������������������������������������  123 10 In Silico Experiments������������������������������������������������������������������������������  135 11 Novel Landscapes������������������������������������������������������������������������������������  159 12 Where to Go from Here?������������������������������������������������������������������������  189

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Resources����������������������������������������������������������������������������������������������������������  195 Glossary������������������������������������������������������������������������������������������������������������  209 Glossary References����������������������������������������������������������������������������������������  213 Index������������������������������������������������������������������������������������������������������������������  215

Abbreviations

ANOVA BACI BDFFP CA DRI-Grass EBP EDGE EDI ELA EMS FUTURES GAM GB GIS GLM G-TREE GUD HPD IALE IMGRE LTER MOFEP MS(E) MS(T) NEON ODD RAM ROV SAFE

Analysis of Variance Before-After-Control-Impact Biological Dynamics of Forest Fragments Project Cellular Automata Drought and Root Herbivore Impacts in a Grassland Experimental Burn Plot Extreme Drought in the Grasslands Experiment Equity, Diversity and Inclusion Experimental Lakes Area Expected Mean Squares FUTure Urban-Regional Environment Simulator Generalized Additive Model Gigabyte Geographic Information System(s) General Linear Model Global Treeline Range Expansion Experiment Giving-up Density Hierarchical Patch Dynamics International Association of Landscape Ecology Inner Mongolian Grassland Removal Experiment Long-Term Ecological Research Missouri Ozark Forest Ecosystem Project Mean Square Error Mean Square Treatment National Ecological Observational Network Overview-Design Concepts-Details Random-Access Memory Remotely-Operated Vehicle Stability of Altered Forest Ecosystems

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SD SDM SEARCH SMS USDA VR

Abbreviations

System Dynamics Species Distribution Model Spatially Explicit Animal Response to Composition of Habitat Stochastic Movement Simulator United States Department of Agriculture Virtual Reality

List of Figures

Fig. 3.1 The effect of experimental type on internal vs. external experimental validity, and the relationship to theory (from which deductive hypotheses originate) and observation (from which inductive hypothesis originate). Experiments with high internal validity will better validate theory, and those with high external validity will better validate patterns observed in nature. The different experimental types discussed in the subsequent chapters of this book are indicated in the box at the bottom and all along a spatial continuum from small to large extent. (Figure adapted with permission from Naeem (2001))��������������������  29 Fig. 4.1 (a) Hypothetical landscape ecology study design, with three forest stands that are otherwise similar, but differ in their time since fire. Twenty sample sites (black dots) are randomly placed within each stand. At each site, the researcher employs a point-quarter technique with four 1 m × 1 m plots (inset circle) to sample ground vegetation. (b) The same hypothetical landscape as in Fig. 4.1a, but with the addition of an environmental gradient (this could be elevation, moisture, distance from a anthropogenic impact). The researcher allocates the 20 sample sites along two parallel transects within each stand��������������������������������������������������  40 Fig. 5.1 Example of a space-time diagram showing the hierarchical nature of disturbance regimes, biotic responses and vegetation patterns. (Reproduced from Delcourt et al. (1982) with permission from Elsevier)����������������������������������������������������������������  56

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Fig. 6.1 Aerial image of one replicate of the experimental design at the Savannah River site. The patch in the foreground, labelled “unconnected rectangular” is 100 × 100 m. Photo by Ellen Damschen (2013) Landscape Corridors, in Encyclopedia of Biodiversity, second edition with permission from Elsevier������������  74 Fig. 7.1 Aerial image of the Bowling Green Fragmentation Model Landscape System near Bowling Green State University, Ohio, USA. (Used with permission from Oxford University Press and Kim With)������������������������������������������������������������������������  92 Fig. 7.2 Diagram of the Kansas University Fragmentation Experiment. (Original figure from Schweiger et al. (2000) and used here with permission of Wiley Ltd.)��������������������������������������������������������  93 Fig. 8.1 Diagram of the mesocosm set up (one replicate) used by Pitcher and Soluk (2016). The length of the PVC pipe connecting the two barrels (“patches”) is experimentally varied to see how length affects crossing events by predators between the two patches. (Figure is licensed under Creative Commons Attribution License CC BY 4.0)�����������������������������������������������������������������������  116 Fig. 8.2 Diagram of the mesocosm set up (one replicate) used by Väisänen et al. (2020). Panel a shows the dimensions of the mesocosm, which is divided into a smaller permafrost compartment and a larger active layer compartment. Panel b shows the actual mesocosm, which is made of acrylic plastic. The treatment manipulates the barrier between the compartments; the left-hand image shows a solid barrier (hermetic treatment) and the right-hand photo shows the 2 mm mesh treatment. Pancel c shows the mesocosm with the active layer compartment filled with peat sod and mosses on the left side and the permafrost compartment filled with Styrofoam as an inert substance and recently thawed and homogenized permafrost soil next to the mesh barrier. (Reproduced from Väisänen et al. (2020) and used here with permission from Elsevier)������������������������������������������������������  117 Fig. 10.1 The relationship between model complexity and model error. Reproduced with permission from Saltelli (2019) who suggests this figure hang above every modeller’s desk. Models that are too simple may be inadequate and have high model error (red line); however, added complexity can lead to error propagation (blue line). Overall modelling error (green line) is the result of both sources of error. (Used with permission of the author and under CC-BY 4.0 License)��������������������������������  137

List of Figures

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Fig. 10.2 The relationships between pattern and process in landscape models. The left side of the figure shows how pattern data can be analyzed deductively to infer processes using descriptive/statistical models), while the right side of the figure illustrates how process models can be built based on deductive hypotheses to predict pattern data (using mechanistic/ mathematical models). (Adapted from Figure 1 in Brown et al. (2006) and reprinted with permission of the publisher, Taylor and Francis Ltd.)�����������������������������������������������������������������  139 Fig. 11.1 A schematic 3D cube of a seascape, illustrating structural pattern, including patches and gradients. Image created by Simon J. Pittman. Used under CC BY-SA 4.0 License������������  161 Fig. 11.2 A schematic of a soundscape, composed of biophony (green stars), geophony (blue stars) and anthrophony (brown stars). (Photo by Yolanda Wiersma)����������������������������������  171

List of Tables

Table 3.1

Taxonomy of landscape ecology experiments as developed by Jenerette and Shen (2012). See Table 1 in their paper for example papers of each of the 15 types of experiments�������������� 30

Table 4.1

Expected mean squares for two factor ANOVA with fixed factor treatment, T, which has a levels, b levels of site S nested within treatments (as a random effect) and n replicates of S per T���������������������������������������������������������������� 41 Expected mean squares for tests for single-factor ANOVA with fixed factor treatment, T, which has a = 3 (3 stands each with time since fire of 10, 50 and 100 years), levels, and n = 80 (sample plot) replicates��������������������������������������������������� 41 Expected mean squares for two factor ANOVA with fixed factor treatment, T (time since fire) and S (site)���������������������������������������������������������������������������������������� 41 Expected mean squares for two factor ANOVA with fixed factor treatment T, which has a levels����������������������������� 43

Table 4.2

Table 4.3 Table 4.4 Table 6.1

Table 6.2

Taxonomy of types of landscape experiments (sensu Jenerette & Shen, 2012), with bold font in the example column indicating the type of experiment for which large-scale manipulations are especially-well suited, and italic font for those types which it may be possible to harness large-­scale manipulations, but for which other experimental approaches may be better suited. References describing examples of large-scale manipulative experiments of each type are given; these are not exhaustive������������������������������� 75 Comparison of experimental designs of the large-scale fragmentation experiments discussed in this chapter����������������������� 79

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List of Tables

Table 7.1

Taxonomy of types of landscape experiments (sensu Jenerette & Shen, 2012), with bold font  indicating the type of experiment for which experimental model landscapes are especially-­well suited, and italic font for those types which it may be possible to harness these, but for which other experimental approaches may be better suited. References describing examples of experimental model landscapes of each type are given; these are not exhaustive����������������������������������������������������������������������������������� 94

Table 8.1

Characteristics used in this book to distinguish between mesocosms, microcosms and micro-landscapes as experimental systems����������������������������������������������������������������� 106 Taxonomy of types of landscape experiments (sensu Jenerette & Shen, 2012), with bold font in the example column indicating the type of experiment for which mesocosm experiments are especially-well suited, and italic font for those types which it may be possible to harness mesocosms, but for which other experimental approaches may be better suited. References describing examples of mesocosm experiments of each type are given; these are not exhaustive������������������������������������������������� 106

Table 8.2

Table 9.1

Taxonomy of types of landscape experiments (sensu Jenerette & Shen, 2012), with bold font in the example column indicating the type of experiment for which microcosm experiments are especially-well suited, and italic font for those types which it may be possible to harness mesocosms, but for which other experimental approaches may be better suited. References describing examples of mesocosm experiments of each type are given; these are not exhaustive������������������������������������������������������������������ 125

Table 10.1 General overview of some of the strengths and limitations of the four categories of modelling methods outlined by Zvoleff and An (2014). Table is reproduced with permission from Zvoleff and An (2014)��������������������������������� 140 Table 10.2 Comparison of attributes of model types discussed in this chapter���������������������������������������������������������������������������������� 141

Part I

Philosophy and Concepts of Experimentation

Chapter 1

What Is Landscape Ecology? Why Do We Need a Book About Experimentation?

1.1  What Is Landscape Ecology? Landscape ecology is a relatively new discipline, although Wiens et al. (2007) trace its roots (particularly in Europe) to the first half of the 1900s in fields such as geography and soil science. The flagship journal Landscape Ecology has been in existence since 1987, which makes it much newer than the Ecological Society of America’s Ecology (first published in 1920) or the British Ecological Society’s Journal of Ecology (in existence since 1913). A recent retrospective of articles published in Landscape Ecology summarizes some of the key concepts in landscape ecology research over the first three decades of the journal; these include pattern analysis, land use/land cover change, disturbance, scaling, and fragmentation/connectivity (Wu, 2017). In their collection of foundational papers in landscape ecology, Wiens et al. (2007, p. 2) describe landscape ecology as “a vital area of research and practice”. They describe how the discipline has focused on understanding the links between spatial patterns and ecological process, a key concept that is echoed in other seminal articles (e.g., Turner, 1989, 2005; Wu & Hobbs, 2002; Wu, 2017). What these previous works have not discussed at length is how to do experiments in landscape ecology. This volume seeks to examine how the unique aspects of landscape ecology require a particular approach to experimentation, and will illustrate the myriad possibilities for conducting experimental work in landscapes.

1.2  Who Is This Book for? In the next section, I will provide a very brief overview of the key concepts in landscape ecology. If you are reading this book, I am assuming you have a reasonably solid background in landscape ecology already and are familiar with some or all of these concepts. You may have taken a university-level course on the topic, or © Springer Nature Switzerland AG 2022 Y. F. Wiersma, Experimental Landscape Ecology, Landscape Series 29, https://doi.org/10.1007/978-3-030-95189-4_1

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1  What Is Landscape Ecology? Why Do We Need a Book About Experimentation?

participated at an International Association of Landscape Ecology (IALE) meeting somewhere in the world. If you are picking up this book because you are interested in learning more about landscape ecology generally, then I suggest you read one of the key texts first (e.g., Farina, 2006; Wiens et al., 2007; Turner & Gardner, 2015; With, 2019; Francis et al., 2021), which will give much more detail than I can provide here. You can also consult the “Resources” section at the back of the book to learn more. For those still new to the discipline, I have indicated terms defined in the glossary in bold font throughout the book. This book is primarily for graduate students and early-career researchers in landscape ecology, who may be interested in applying an experimental approach to their research. Established landscape ecology researchers likely have techniques for doing their science that works for them; it may include one or more of the experimental approaches highlighted in the second half of this book. However, they may find that this book may help them to adapt what they have always been doing to be more explicitly experimental, or to develop complementary approaches to what they already do that can help increase their ability to make strong inferences.

1.3  Key Concepts in Landscape Ecology Landscape ecology is a branch of ecology that emphasizes the links between spatial pattern and ecological processes (Turner, 1989, 2005), and seeks to understand how ecological processes both shape, and are shaped by, these patterns. Other branches of ecology try to link patterns and processes at the levels of populations, communities and ecosystems, but what makes landscape ecology unique is the emphasis on spatial context. Analyses tend to be spatially explicit, rather then spatially implicit or aspatial. Unlike other branches of ecology, which seek relatively homogenous environments to work within (e.g., the community ecology of a single pond), landscape ecologists explicitly embrace spatial heterogeneity. The “patch-mosaic model” (Wu, 2013a), which carries the axiom that the sum is greater than the parts, is a guiding (but not an exclusive) theme for the discipline. As noted by Wiens et al. (2007) and With (2019), the intellectual roots of landscape ecology are somewhat different between Europe and North America. The focus of North American landscape ecology is more ecological/biological, and highly influenced by island biogeography theory and conservation issues. The European “school” of landscape ecology is more geographically influenced, and focuses on a holistic integration of research from both physical and cultural geography (Wu & Hobbs, 2007). Although not universally true, North American research has tended to focus more on natural/ wilderness landscapes, while European research has focused more on cultural landscapes. The distinction between the two “schools” of thought on the discipline is not a hard boundary, and landscape ecology has become a global discipline (With, 2019). While my training and research is influenced by the North American “school” of landscape ecology (although I have interacted and collaborated with European colleagues at points in my career), I have tried, in this volume, to integrate examples

1.3  Key Concepts in Landscape Ecology

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and research from around the globe in order to provide as broad a perspective as possible. Landscape ecology work has, for the most part, been carried out at kilometre-­ wide extents (Wu, 2013a, 2017), and has integrated field sampling with analyses using data and tools from remote sensing and geographic information systems (GIS). While the default is to perceive the discipline as focused on terrestrial landscapes, this is not a limiting factor. The discipline includes studies that are carried out in aquatic (“riverscapes”) and marine (“seascapes”) systems and more recently, has explicitly embraced urban landscapes (Wu et al., 2013). Much of the early work on landscape ecology has focused on developing the tools for quantifying and describing spatial patterns and the links between patterns and processes. Technical developments related to scale and the hierarchical structure of landscapes, along with developments in modelling and spatial analysis, have occupied much of the field’s attention. Key concepts with links to the field of conservation biology have included research on developing our understanding of landscape fragmentation and connectivity, land cover change, interactions with climate change and other natural and anthropogenic disturbances, and with ecosystem services (Wu & Hobbs, 2002; Wu, 2013a, 2017). Landscape ecology also prides itself on being an “interdisciplinary” discipline, or even a transdisciplinary one (Tress et al., 2005). Unlike other branches of ecology, landscape ecology explicitly includes humans and their impacts on the landscape as an object of study; indeed the “shortcut” definition of a landscape as “what you can see from an airplane window” includes land uses as one of the three components of what makes up a landscape (along with land forms and land cover). Because of this explicit inclusion of humans and their use of the land, landscape ecologists often collaborate closely with social scientists such as economists, planners, or historians; this is a cross-disciplinary divide that other fields (such as conservation biology) have cited as being highly necessary to bridge (Bennett et al., 2017) in order to solve the world’s major challenges. Landscape ecologists may have training in various fields, including (but not limited to) ecology, earth science, geography, geomatics, soil science, planning, design, or computer science. You can find academic landscape ecologists in university departments ranging from landscape architecture and planning, to natural resource management, geography and biology. Landscape ecology is also a highly applied discipline; much of the research focus is on contributing to management issues around forests, wildlife, agriculture and urban areas. More recently, the development of research in landscape sustainability science has emphasized the linkages between understanding landscapes and ensuring sustainability of ecosystem services (Wu, 2013b). Without a doubt, landscape ecology as a discipline has expanded and diversified over the past few decades (Wu & Hobbs, 2002; Wu, 2017).

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1.4  Why Experiments? In the introduction to their collection of “foundation papers”, Wiens et al. (2007, p. 2) describe landscape ecology as a field that is “testing the generality of its concepts across systems and scales”. In the realm of science, we test ideas via experimentation. However, despite over thirty years of development of landscape ecology as a discipline and many excellent synthetic books on various topics germane to landscape ecology, we have little to guide us on how to do experiments. Early scientists in chemistry, physics, and physiology became comfortable with experimental approaches much earlier than those who were working in ecological systems. From the earliest days (and even up to modern times), there have been tensions within ecology about how much emphasis to place on holistic natural history approaches to knowing, vs. reductionist, empirical, and experimental approaches (Kohler, 2002; Guidetti et al., 2014). There are many general texts on doing experiments in ecology broadly (see Resources section of this book), but the spatial complexity of landscapes means that many of these experimental approaches do not translate easily into spatially explicit studies. With the exception of an edited collection on “Real-world ecology” (Miao et al., 2009), which tackles some of the issues of large-scale experimentation, there are few resources to help landscape ecologists design effective experiments. Is it so important that we have experiments in landscape ecology? I would argue that it is. Experiments provide strong evidence in support of a particular issue. Landscape ecology has had, and will likely continue to have, an important role to play in informing policy and management decisions (Mayer et  al., 2016). Much research in landscape ecology touches on the critical ecological, environmental, conservation and sustainability challenges in our society today. By developing and applying robust experiments, we as scientists can provide an evidence-based approach to decision makers that can counter the proliferation of rumours, counter-­ factual arguments and conspiracy theories that proliferate in today’s modern world.

1.5  Overview of This Book Following this introductory chapter, I have organized the book into two main parts. The first (Philosophy and Concepts of Experimentation) discusses some of the broad issues germane to experimental approaches to the generation of knowledge. Experiments are only one form of knowledge generation, but are at the core of doing science. In Chap. 2, I briefly discuss the history and philosophy of science and the role of experimentation in the development of modern science. This chapter will trace some of the earliest attempts to develop experimental approaches to ecological study, while also providing an outline of the criteria for a good experiment. In Chap. 3, I explore how the unique nature of landscape-scale studies can make it difficult to meet the criteria for good experimental design outlined in Chap. 2. I will highlight

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what others have said about large-scale experiments (e.g., Miao et  al., 2009; Jenerette & Shen, 2012; Barley & Meeuwig, 2017) and identify broad-level considerations for those thinking about doing landscape ecology experiments. Chapters 4 and 5 give further guidance on two issues particularly relevant to experimental design in landscape ecology—challenges with pseudoreplication (Chap. 4) and issues of scale (Chap. 5). Although much has already been written about scale issues in landscape ecology (Delcourt et al., 1982; Urban et al., 1987; Wiens, 1989; Wu, 1999; Jackson & Fahrig, 2015; Dixon Hamil et al., 2016; Gholz & Blood, 2016; Newman et al., 2019), the focus in this chapter is on how scale issues affect experimental design. Chapter 4 attempts to carefully dissect the highly cited paper on pseudoreplicaton by Hurlbert (1984) and provides a commentary on the various critiques that followed. More usefully (I hope), it provides worked-out examples of how to partition error in experimental design to avoid accusations of pseudoreplication. The second half of the book (Approaches to Experimentation) includes six chapters, each of which focuses on a particular experimental technique. Within each chapter, I provide case examples of experiments that illustrate how one can harness the technique for landscape ecology experiments. Not all of the case studies highlighted are explicitly landscape ecology studies. Some treat space implicitly, or apply a community- or population-level question across a broad spatial extent. Nonetheless, cumulatively, I hope that the examples are illustrative of what is possible. Chapter 6, on large-scale manipulative experiments, and Chap. 7, on what I am calling experimental model landscapes, include the types of studies that most landscape ecologists likely think of when they think of landscape experiments. These happen on the scale of hectares to kilometres. To discuss them broadly, I have set a somewhat arbitrary threshold to include studies with extents greater than 15 ha in Chap. 6 and those less than this in Chap. 7. Although the majority of landscape ecology studies are on the scales of tens to thousands of kilometres, Wiens and Milne (1989) argued that scaling down could have advantages for research. Despite the fact that Wiens and Milne (1989) argued for “sandbox” experiments over three decades ago, there have not been many small-­ extent landscape ecology studies. However, our colleagues in community ecology have made all kinds of creative and innovative use of mesocosms and microcosms around the globe. In Chaps. 8 and 9, I present examples of mesocosm and microcosm work, respectively, that either have addressed a spatial question, or could be harnessed to do so. Here, I differentiate mesocosms (the subject of Chap. 8) as being within artificial containers (e.g., tanks or buckets) and microcosms (discussed in Chap. 9) as naturally occurring contained environments (e.g., pitcher plants, tide pools). Landscape ecologists have never shied away from computers as a research tool, and in Chap. 10, I highlight the myriad ways that the in silico environment can be harnessed for experiments, whether these be statistical or mathematical approaches, or cellular automata, agent-based or system dynamic models. Although landscape ecology has expanded into aquatic and acoustic landscapes, doing experiments in these environments may be a little bit different. Thus, Chap. 11 delves into brave

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new worlds for landscape ecology experiments. I explore how experiments in seascapes, riverscapes and soundscapes may offer opportunities to ask different kinds of questions, while also carrying different challenges and advantages compared to experiments in terrestrial systems. Finally, in this chapter, I explore new ideas for sub-organismal landscape ecology within our own bodies. To try to make this book as useful as possible, I have synthesized my thinking in the final chapter. However, I do not think this is the final word on the topic. Because I believe our discipline is only beginning to explore what is possible with experimentation, I have focused on providing an extensive “Resources” section at the end of the book. Throughout the book, I highlight where to find information that may be useful to anyone who may wish to try some of the experimental approaches described. I hope that cumulatively, the book and resources spur many new, creative approaches to experiments in landscape ecology, and I look forward to seeing the results of these published in the pages of journals, and perhaps future books.

References Barley, S. C., & Meeuwig, J. J. (2017). The power and the pitfalls of large-scale, unreplicated natural experiments. Ecosystems, 20, 331–339. https://doi.org/10.1007/s10021-­016-­0028-­5 Bennett, N. J., Roth, R., Klain, S. C., et al. (2017). Mainstreaming the social sciences in conservation. Conservation Biology, 31, 56–66. https://doi.org/10.1111/cobi.12788 Delcourt, H.  R., Delcourt, P.  A., & Webb, T. (1982). Dynamic plant ecology: The spectrum of vegetational change in space and time. Quaternary Science Reviews, 1, 153–175. https://doi. org/10.1016/0277-­3791(82)90008-­7 Dixon Hamil, K. A., Iannone, B. V., Huang, W. K., et al. (2016). Cross-scale contradictions in ecological relationships. Landscape Ecology, 31, 7–18. https://doi.org/10.1007/s10980-­015-­0288-­z Farina, A. (2006). Principles and methods in landscape ecology: Towards a science of landscape. Springer. Francis, R. A., Millington, J. D. A., Perry, G. L. W., & Minor, E. S. (Eds.). (2021). The Routledge handbook of landscape ecology. Routledge. Gholz, H. L., & Blood, E. R. (2016). MacroSystems biology: Stimulating new perspectives on scaling in ecology. Landscape Ecology, 31, 215–216. https://doi.org/10.1007/s10980-­015-­0300-­7 Guidetti, P., Parravicini, V., Morri, C., & Bianchi, C. N. (2014). Against nature? Why ecologists should not diverge from natural history. Vie Milieu, 64, 1–8. Hurlbert, S. H. (1984). Pseudoreplication and the design of ecological field experiments. Ecological Monographs, 54, 187–211. https://doi.org/10.2307/1942661 Jackson, H.  B., & Fahrig, L. (2015). Are ecologists conducting research at the optimal scale? Global Ecology and Biogeography, 24, 52–63. https://doi.org/10.1111/geb.12233 Jenerette, G.  D., & Shen, W. (2012). Experimental landscape ecology. Landscape Ecology, 27, 1237–1248. https://doi.org/10.1007/s10980-­012-­9797-­1 Kohler, R.  E. (2002). Labscapes and landscapes: Exploring the lab-field border in biology. University of Chicago Presss. Mayer, A. L., Buma, B., & Davis, A. D., et al. (2016). How landscape ecology informs global land-­ change science and policy. BioScience, 66, 458–469. https://doi.org/10.1093/biosci/biw035 Miao, S., Carstenn, S., & Nungesser, M. (Eds.). (2009). Real world ecology: Large-scale and long-­ term case studies and methods. Springer.

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Newman, E.  A., Kennedy, M.  C., Falk, D.  A., & McKenzie, D. (2019). Scaling and complexity in landscape ecology. Frontiers in Ecology and Evolution, 7, 293. https://doi.org/10.3389/ fevo.2019.00293 Tress, G., Tress, B., & Fry, G. (2005). Clarifying integrative research concepts in landscape ecology. Landscape Ecology, 20, 479–493. https://doi.org/10.1007/s10980-­004-­3290-­4 Turner, M. G. (1989). Landscape ecology: The effect of pattern on process. Annual Review of Ecology and Systematics, 20(20), 171–197. https://doi.org/10.1146/annurev.es.20.110189.001131 Turner, M. G. (2005). Landscape ecology in North America: Past, present, and future. Ecology, 86, 1967–1974. https://doi.org/10.1890/04-­0890 Turner, M. G., & Gardner, R. H. (2015). Landscape ecology in theory and practice: Pattern and process. Springer. Urban, D. L., O'Neill, R. V., & Shugart, H. H. (1987). Landscape ecology: A hierarchical perspective can help scientists understand spatial patterns. Landscape Ecology, 37, 119–127. Wiens, J.  A. (1989). Spatial scaling in ecology. Functional Ecology, 3, 385–397. https://doi. org/10.2307/2389612 Wiens, J. A., & Milne, B. T. (1989). Scaling of “landscapes” in landscape ecology, or, landscape ecology from a beetle’s perspective. Landscape Ecology, 3, 87–96. https://doi.org/10.1007/ BF00131172 Wiens, J. A., Moss, M. R., Turner, M. G., & Mladenoff, D. J. (Eds.). (2007). Foundation papers in landscape ecology. Columbia University Press. With, K. A. (2019). Essentials of landscape ecology. Oxford University Press. Wu, J. (1999). Hierarchy and scaling: Extrapolating information along a scaling ladder. Canadian Journal of Remote Sensing. https://doi.org/10.1080/07038992.1999.10874736 Wu, J. (2013a). Key concepts and research topics in landscape ecology revisited: 30 years after the Allerton Park workshop. Landscape Ecology, 28, 1–11. Wu, J. (2013b). Landscape sustainability science: Ecosystem services and human well-being in changing landscapes. Landscape Ecology, 28, 999–1023. https://doi.org/10.1007/ s10980-­013-­9894-­9 Wu, J. (2017). Thirty years of landscape ecology (1987–2017): Retrospects and prospects. Landscape Ecology, 32, 2225–2239. https://doi.org/10.1007/s10980-­017-­0594-­8 Wu, J., & Hobbs, R. (2002). Key issues and research priorities in landscape ecology: An idiosyncratic synthesis. Landscape Ecology, 17, 355–365. https://doi.org/10.1023/A:1020561630963 Wu, J., & Hobbs, R. (2007). Landscape ecology: The state-of-the-science. In J. Wu & R. Hobs (Eds.), Key topics in landscape ecology (pp. 271–287). Cambridge University Press. Wu, J., He, C., Huang, G., & Yu, D. (2013). Urban landscape ecology: Past, present and future. In B. Fu & K. B. Jones (Eds.), Landscape ecology for sustainable environment and culture (pp. 37–53). Springer.

Chapter 2

What Does It Mean to Do Experiments in Ecology? Historical Context and Current Approaches

Science, for me, gives a partial explanation for life. In so far as it goes, it is based on fact, experience and experiment. Rosalind Franklin

2.1  Introduction In movies, children’s TV shows, and comic strips, portrayals of scientists usually show them as white-haired men, wearing glasses and lab coats, perched behind a bank of vials, test tubes and beakers, which contain liquids of various colours that are spewing steam and smoke. Often, at some point there is an explosion. In this book, I am not going to unpack the problem with the fact that many people hear “scientist” and think of a white male. The challenges of making STEM accessible to women, people of colour, people who are differently abled or with diverse sexual orientations and identities is an important one. It is an issue I care about on a personal level, but not one that I am qualified to discuss academically. However, I have provided a link for more information, and a list of readings on the topic of equity, diversity and inclusion (EDI) in science in the Resources section of the book. The point is that most people have only seen a “scientific experiment” as portrayed by Hollywood and imagine it can only happen in a lab with chemistry-type apparatus. Ecologists are scientists too, and this book is for ecologists, specifically landscape ecologists. If you are an ecologist, and you tell people you are doing science, it may take them a minute to reconcile this image of the white-coated scientist behind their glassware with your explanation that you do not work in a lab, or that you do not use chemicals and Bunsen burners (not to say that some ecologists do not do bench work). If you specify that you are an ecologist, and mention that you “do field work”, then suddenly the image in the lay person’s mind changes to a scientist clad in khaki, wearing sturdy shoes, carrying either a bug net or a pair of binoculars, striding off into a meadow. While such an image may (but does not necessarily have to) come a little closer to what it looks like to “do ecology” than the image of the © Springer Nature Switzerland AG 2022 Y. F. Wiersma, Experimental Landscape Ecology, Landscape Series 29, https://doi.org/10.1007/978-3-030-95189-4_2

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scientist in the exploding lab, most lay people would have a hard time seeing how “birdwatching” or “collecting bugs” could be the equivalent to “doing experiments”. These tensions between bench work and field work date back to the earliest days of ecology (more on that below). Although this book is not a comprehensive history or philosophy of science (for excellent readings on those topics, please see the “Resources” at the end of the book), a short summary of the development of experimentation in science more broadly is warranted here. This chapter provides a short history of science, and then outlines our current approaches to doing experiments, along with the key criteria for a good experiment. The next chapter contrasts these general guidelines with the practical challenges of applying them in landscape ecology work. In Part II of the book I will describe different ways of doing landscape ecology experiments, and assess how each can meet these key criteria of good experimentation in different experimental contexts.

2.2  A Short History of Scientific Experimentation How did scientists develop the need to do experiments in any case? Although the word “scientist” was not formalized until the British Association of the Advancement of Science used it in 1884 to describe “students of nature” (Gauch, 2003), inquiries into how the natural and physical world work can be found going back to the early Greeks through to the Middle Ages. Early medieval scholars introduced significant approaches to advance science out of its roots in philosophy and religion. Robert Grosseteste (c. 1168–1253) may not be as familiar an historical figure as Aristotle or Plato, but he played a significant role in advancing science beyond the early philosophers. Grosseteste was a key figure in bringing about a shift from philosophical musings to explaining natural phenomena to one based on empirical evidence using a combination of controlled experiments accompanied by mathematical descriptions. In short, Grosseteste invented the scientific method (Gauch, 2003). His approach had a ripple effect on science, as Newton was heavily influenced by Grosseteste’s approach of inductively deriving generalizations from many repeated observations, and deductively making predictions about future events based on these generalities. Grosseteste called his method the “Method of Resolution and Composition” which meant that it had both inductive and deductive components. Although Aristotle had originally articulated an inductive-deductive view of the world, Grosseteste built on it. Grosseteste’s approach was to subject theories to rigorously controlled experiments to see if outcomes and data met expected predictions. By prioritizing data over theories, the experimental method could eliminate theories when data showed them to be false (Gauch, 2003). Grosseteste’s approaches closely resemble the philosophical positions of Karl Popper (1902–1994), which I summarize briefly in the section below on the principle of falsification. Ecology as a science began to develop around the late 1800s into the early 1900s. Early tensions amongst scientists centred on whether ecology was a “real science” or just something done by natural history hobbyists (Kohler, 2002). A natural

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history approach to ecology focused on describing and identifying species, and any inferences about underlying mechanisms were qualitative and based strictly on observations made in the field, and not on any kind of experiment. On the other hand, a scientific approach sought to explain cause-and-effect through experiments and quantitative methods. Because “bench science” in biology, particularly in physiology and genetics was developing rapidly at this time, there was debate as to whether science could be conducted in the natural world, and whether experiments that were not carried out within the confines of the lab were valid (Kohler, 2002). As a consequence of these views, early “experimental work” within the nascent field of ecology focused on rigorous quantification of natural systems, exemplified by Frederic Clements’ handbook on ecological methods, which was published in 1905 (Clements, 1905). Quantification of natural patterns and phenomena helped give the burgeoning field of ecology scientific credibility and to move beyond the perception that it was simply a weekend hobby, carried out by people who enjoyed spending time in nature. Indeed, Clements was influential in bringing approaches that were more rigorous to ecological research beyond what was previously descriptive natural history. Clements was the co-inventor (with Roscoe Pound) of one of the most commonly used pieces of technology in ecological field experiments—the quadrat. Although quadrat sampling is decidedly low tech—after all a quadrat can be constructed inexpensively out of everyday materials—the notion that nature could be systematically counted and sampled, and that doing so through quadrats could provide insights into a larger region, was radical for its time. Clements was instrumental (pun intended) in making field ecology more scientific. Trained in laboratory methods, he saw the value of introducing tools for rigorous measurement to field biology. He was notorious for availing himself  of various items that would have represented cutting-edge technology in his day (for example, soil thermographs, anemometers, photometers, barometers and microscopes). Apparently, his propensity for spending department funds on field instruments had his colleagues at the University of Minnesota quite angry with him (Kohler, 2002)! No doubt, if he were a practicing ecologist today, he would be equipped with the latest drones, precision GPS units, and remote cameras. The first generation of ecologists (from the late 1890s to ca. 1950) struggled to conduct experiments in the field (Kohler, 2002). They carried out most hypothesis testing through what we now might call “observational experiments”. An early example of one such observational experiment, one with a definite landscape ecology bent (but before the discipline of landscape ecology was formalized), is the work of Forrest Shreve, who used mountain systems to try to measure and explain which environmental factors drive vegetation patterns. In a short piece in Science (Shreve, 1916), he describes “Experimental work at Cinchona [a mountain station in the Blue Mountains, Jamaica]”. He describe the site as having high diversity of vegetation and temperature and moisture conditions and thus amenable to studying the relationships between environment and plant distribution. He suggests research possibilities in what we would now call physiological ecology and community ecology, and points out that nearby greenhouses and gardens provide facilities for more controlled studies that could complement the field observations (Shreve, 1916). His

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book (Shreve, 1915), derived from a long-term study at Cinchona contains detailed vegetation species lists, coupled with tables of rainfall patterns through space and time, and graphs that details how moisture regimes change with elevation. Some straightforward description of how these vary on north vs. south-facing slopes provides the only analytical component to the study. Despite being largely descriptive, Shreve’s (1915) work illustrates some early thinking along experimental lines. In the concluding section of the book, he tries to integrate the patterns of vegetation with potential environmental drivers. Ultimately, he concluded that it would be easier to understand plant distributions if studies could be “(o)n a mountain having the form of a smooth cone” (Shreve, 1915, p. 110) because variation in soils, topography and presence of streams on real mountains confounds any regular patterning. Despite that Shreve lacked a model system of a perfectly conical mountain (see Chaps. 9 and 11 for a discussion of how we apply model systems in landscape ecology), his detailed observations do lead to some insights gained by “the correlation between [the vegetation gradient and the climatic gradient]” and help to “indicate some of the physical controls which operate in the limitations of the ranges of species” (Shreve, 1915, p. 112). The historian of science Kohler (2002, p. 155) concludes that “[Shreve] believed ardently in experiment, but his attempts to practice what he preached fell well short of the ideal.” This may be overly harsh; Shreve was motivated to do field experiments, yet he ultimately found he was mostly limited to descriptive observations. In many ways, Shreve’s observational study is not dissimilar from current research—a recent keyword search on “vegetation” AND “elevation” AND “gradient” in the journal index Scopus, yields just over 2000 citations! There has been other important work on gradient analysis since, that form a huge part of community ecology and ecology more broadly (e.g., Whittaker, 1967; Peet & Loucks, 1977) and that have had an influence on landscape ecology (McDonnell & Hahs, 2008; Evans & Cushman, 2009; Cushman et  al., 2010). Naturally there have been advances on Shreve’s simple field measurements and descriptive correlations; scientists still study vegetation gradients but make use of more advanced tools and technologies than Shreve had, including remote sensing (e.g., Liu et al., 2019), stable isotopes (e.g., Jaeschke et al., 2019) and multivariate statistics (e.g., Anwar et al., 2019). However, most share in common with Shreve that they are observational experiments and not strict manipulative experiments. Through these endeavours, ecologists began to consider the idea of using space as snapshot for time (what we now call “space-for-time-substitutions”). Researchers realized that the process of succession took too long to observe within a reasonable amount of time, but that by sampling vegetation along a gradient of disturbance, for example along shifting sand dunes, one could “see” change through time as one moved from the newer fore dunes away from the shore to older back dunes. Areas from which glaciers had retreated were also an area where the process of succession could be seen across space. One interesting example of the latter is the work of William Cooper in Glacier Bay, Alaska who studied how vegetation occupied new ground as the glacier retreated. In three articles spread across consecutive issues of Ecology, he details his excitement about “the opportunity to study the successional process directly” (Cooper, 1923a, p.  93) instead of relying on comparative work

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using different locations at different successional stages. He noted that by collaborating with geologists, who could assist with interpreting how long an area had been exposed, one could estimate past vegetation succession events. Moreover, he noted that the development of plant communities was sufficiently rapid to allow for changes to be observed over five years (Cooper, 1923a). To that end, he harnessed the then cutting-edge tool of the quadrat to establish nine permanent sampling plots in 1916, which he then resurveyed in 1921. His paper carefully documents changes in plant species composition over this time, including spatial distribution, abundance, and growth forms (Cooper, 1923b). He readily acknowledges the value of these permanent plots over past observational studies; pointing out that comparing vegetation across sites is “largely inferential to the sequence of stages and details of development” (Cooper, 1923b, p. 355) while the revisiting of quadrats allows for accurate data on plant populations and successional pathways. What makes this story particularly interesting for modern landscape ecologists is that at the 2018 US-IALE meeting in Chicago, contemporary landscape ecologist Brian Buma presented his recent resurveying work of Cooper’s plots, 100 years later! Cooper had intended that his plots would be re-surveyed every 5 years on a regular basis, and they were up until the 1990s. However, after the death of his graduate student Donald Lawrence, the plots were neglected. Some detective work by Buma and his colleagues—involving comparisons of historical photos with current locations, the use of Cooper’s hand drawn maps and written directions, along with a metal detector to find the iron rods that marked the plot corners (Buma et al., 2017)—relocated the plots. This allowed this new team to continue the survey work that Cooper had initiated long before Buma and his collaborators were born! Buma and colleagues subsequently demonstrated that Cooper’s original idea that successional pathways were related to time since exposure was not completely accurate; successional patterns were strongly influenced by distance to seed sources and local neighbourhood influences, along with stochastic species assemblage (Buma et al., 2017). As the field of ecology advanced, researchers increasingly took advantage of what they termed “Nature’s experiments”, or what we might now call “natural experiments”. One approach to natural experiments was to make use of perturbations as an experimental treatment. Areas that had been affected by a disturbance, whether natural or induced by humans, could be compared to nearby ones that were undisturbed and differences could be attributed to the disturbance force. For example, the creation of the Panama Canal facilitated the development of Lake Gatun in 1913, and former hilltops became islands, including the well-studied Barro Colorado Island. This natural fragmentation of tropical forest due to flooding showed that the island remnants tended to lose species and that this effect was more pronounced for the smaller islands (Leigh Jr. et al., 1993). Such “natural experiments” were often larger-scale and one could describe them as biogeography or landscape ecology studies. In a similar study, ecologists in the 1980s took advantage of the construction of a large dam in Venezuela to look at how species responded to habitat insularization (Terborgh et al., 2001) immediately following fragmentation, in contrast to the Panama study, where some time had elapsed between the flooding and the first surveys. These large-scale ecological experiments fuelled debates over the value of

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natural experiments vs. field manipulations and contrasted these with the rigor (and limitations) of lab based studies (Diamond, 1983). Diamond emerged as a proponent of natural experiments (a.k.a. “observational studies” or “observational experiments”) because they allowed one to examine extreme conditions that would be either difficult, or unethical to manipulate through field-based experiments (Diamond, 2001). Today, ecologists are quite comfortable with studies that move between experiments at the lab bench, manipulative experiments in the field, and observational (“natural”) experiments. Added to this mix are a large range of experiments conducted “in silico” (see Chap. 10). This latter tool was not available to earlier ecologists, given the limitations of early computers. However, the value of mathematical theory was recognized in the early 1980s (Schoener, 1982); theory was seen to both support field experiments and help identify new areas of uncertainty and articulate new hypotheses. Throughout this book, I will provide examples of how each of these various—and often complementary—approaches to experimentation (and others not listed here) are applied to questions in landscape ecology.

2.3  Current Approaches to Experimentation 2.3.1  The Principle of Falsification The modern scientific method is based on the principle of falsification. Unfortunately, the lay public, and even many undergraduates, do not understand this and are under the impression that the job of scientists is to “prove things are true”. Despite that all scientists seek to explain better how the world works, the idea that we are uncovering “the truth” is erroneous. The crux of the hypothetico-deductive approach is that theories can never be proven to be true, they can only be proven to be false, and that one single observation that runs counter to a hypothesis is enough to reject a theory (Popper, 1963). A deductive hypothesis is grounded in theory and predicts which data would support the hypothesis and which would refute it. Repeated experiments that yield evidence in support of the hypothesis can help move that hypothesis closer to a theory; however a single experiment that refutes the hypothesis means that the theory needs to be reconsidered (assuming that the result is not due to a flawed experiment). When scientists “accept a hypothesis”, the more proper way to describe this would be that they are “failing to reject it”. The failure to reject a hypothesis when it is in fact correct is a Type II error. Type II error rates (and Type I error—the probability of rejecting a true null hypothesis) are heavily influenced by the experimental design. Good experiments are difficult to design. While there are excellent books on experimental design for ecology broadly (e.g., Hairston Sr., 1989; Krebs, 1989; Resetarits Jr. & Bernardo, 1998; Karban et al., 2014; see “Resources” section for more details), some of the added complexities of doing landscape ecology make

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experimentation particularly challenging. I will discuss these in more detail in Chapters 3, 4 and 5. Below I give a brief review of the criteria of any good experimental design with examples from ecology broadly. How to apply these characteristics of good experimental design to landscape ecology will be the focus of this book.

2.4  Criteria for a Good Experiment The fundamental elements of any experimental design are control, replication and randomization. In addition, researchers need to consider causal assumptions and the effect of inferences about cause-and-effect (Kimmel et al., 2021). When a researcher achieves these well, they have a good experiment. Control  To allow for falsification, all experiments should have a control. In an experimental sense, a control is a set of observations that are identical to the experiment, except for in the factor of interest. Thus, in a plant growth experiment in a greenhouse to test the effect of a particular fertilizer, the control would be the set of plants that are growing under the same conditions (e.g., same soil, light, water, pot type) as those with the fertilizer added, minus the fertilizer. A control gives the researcher more confidence that any observed effect is due to the experimental manipulations and not to some extrinsic, possibly unknown, factor. In the early days of ecology, it was most common to see rigorous experiments with controls in physiological ecology studies (or “autecology”, to use the parlance of the day). One of the earliest examples of an experimental control applied to a larger scale (“synecological”) study is the Hubbard Brook experiment (Hobbie & Likens, 1973), in which one watershed was denuded of trees and the other left as a control, to assess how water biogeochemistry was affected by deforestation. When evaluating the impact of an anthropogenic disturbance (i.e., environmental impact studies), a common experimental design is to use a BACI (Before-After-Control-Impact) approach (Christie et al., 2020), and such a design has been applied to experimental disturbances as well (e.g., Cooper-Ellis et al., 1999; Fajvan et al., 2006). In field ecological studies, we also use the term “control” to describe an additional experimental manipulation to control for the effects that the manipulation might add to the experiment, or to exclude what Hurlbert (1984) called “nondemonic intrusions” (Koehnle & Schank, 2009) and what Kimmel et al. (2021) refer to as “excludability”. For example, experiments that test the effects of predators and prey frequently use exclosures to keep predators out and compare the behaviour and population growth of prey inside them to a control area where predators are present. However, it can be difficult to ascertain whether the prey response is confounded by the presence of the cage. Thus, many cage experiments have a main treatment—a cage structure that exclude predators, and a “control treatment”, such as an “open cage” that is constructed similarly to the treatment but where predators can enter (Steele, 1996). This allows researchers to tease apart the animals’ response to

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predator exclusion vs. the cage structure itself. Finally, ecological studies are often cautioned about the need to “control for” spatial and temporal variation” (Resetarits Jr. & Bernardo, 1998), although as we will see in this book, in experimental landscape ecology, we are often exploiting spatial (and temporal) variation explicitly. Replication  In introductory statistics, we teach students the importance of replication to capture the variation inherent in a population. We present the mantra as “more replicates is better” as increasing the sample size increases the statistical power. Replication of plants growing in pots in a greenhouse is logistically simple; in ecological systems, replication becomes more complex. For example, the Hubbard Brook experiment, and other experiments looking at disturbance at a large spatial extent, do not have replication. A further complication lies with terminology. In a greenhouse experiment where each pot has a single plant in it that the researcher subjects to either a treatment (fertilizer addition, for example) or a control, the experimental unit is often equivalent to the sampling unit. Experimental units are defined as “the smallest division of the experimental material such that any two units may receive different treatments” (Krebs, 1989, p.  269). Note that “treatments” can mean “treatment combinations”) and that the researcher imposes the treatments in a manipulative experiment but treatments are delineated via different ecological conditions in an observational experiment. Thus if our research question was to determine the effect of added fertilizer to a single shrub growing in a single pot, then each potted shrub would be an experimental replicate. In some cases, an experimental unit may be very large (e.g., a forest stand) and subsamples (e.g., multiple 1 m x 1 m quadrats within a 100 ha stand) are used to collect representative data for the experimental unit. Students (and scientists) often mislabel these subsamples as “experimental replicates”; properly they should be called “subsamples”, or “sampling units”. An experimental unit is thing on which a treatment is applied, and a sampling unit is the thing on which the effect of the treatment is measured. A sampling unit can be identical to an experimental unit; for example, exposing individual potted plants to different fertilizer treatments and then measuring the plant dry matter at the end of the experiment. Or the sampling unit may be a component of the experimental unit – such as the sugar content of a fruit harvested from a plant which was exposed to a fertilizer treatment (Steel & Torrie, 1980). Others have used the term “evaluation unit” (Urquhart, 1981; Hurlbert, 2009) or “observational unit” to distinguish from the experimental unit. Logistical challenges of replicating experimental units and sampling units in the field may mean the number of samples is limited, or that they have to be placed close together. This can lead to issues of spatial autocorrelation (Legendre, 1993) and/or pseudoreplication (Hurlbert, 1984). If samples are dispersed too much, then there may be too much natural variation between sites such that they are not suitable replicates. Spatial arrangement of treatments can contribute to interference; Kimmel et al. (2021) give the example of a random placement of herbivore exclosures where one of the control plots is surrounded by plots with exclosures. They posit that this may change the herbivore’s behaviour on the control plot to the extent that it no longer represents what is typical. Techniques commonly used in ecology to

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overcome this are block sampling and stratified sampling (Hairston Sr., 1989). I will discuss sampling issues germane to landscape ecology experiments including the issues of pseudoreplication and spatial autocorrelation in detail in Chaps. 3 and 4. Randomization  The last element of good experimental design is randomization. Treatments should be applied randomly among experimental units. A lab study where all the vials under one treatment are placed close to the window may see an effect that is caused by exposure to sunlight rather than to the treatment under study! Randomization in ecological field studies usually applies to where, when and how sampling units are measured, and less to experimental units. In natural experiments (e.g., comparing a forest post-fire to an unburned area), the location of the experimental units is determined by nature. Small-scale field manipulations (e.g., multiple warming chambers in a field) may have the luxury of randomizing the treatment among experimental units, but when field manipulations are at large extents (e.g., an entire watershed, such as the Hubbard Brook studies), the replicates of experimental units are limited and hence randomization is more important for the sampling units. With more advanced modelling and statistical techniques, researchers need to put careful thought into sampling design to ensure that assumptions of the models used are not violated. Williams and Brown (2019) describe how sampling design relates to statistical inference. They describe how random sampling leads to design-­ based inference, while model-based inference assumes a hypothesized model for the data, which can accommodate non-randomness and accounts for stochasticity in the sampling units (Williams & Brown, 2019). There are many ways to carry out random sampling; design-based inference can draw on techniques such as cluster sampling, stratified random sampling and systematic sampling (Jongman et  al., 1995). When experimental design cannot eliminate all potential biases, post-hoc analysis may help; Kimmel et al. (2021) discuss analytical approaches to deal with violations of causal assumptions.

2.5  The Bottom Line This chapter presents a brief overview of the evolution of experimentation in ecology broadly in order to appreciate fully the challenges and value of doing experiments within the sub-discipline of landscape ecology. As ecology emerged as a formal scientific discipline in the first half of the nineteenth century, the emphasis on measurement and quantification were what practitioners used to distinguish the burgeoning science from its roots in natural history. From the earliest beginnings, ecologists have sought to understand better the workings of the natural world. As Frederic Clements put it “No study deserves to be called ecological that does not deal with the cause-and-effect relation of habitat and organism in a quantitative and objective manner” (Clements, 1905, quoted in Kohler, 2002, p. 87). This remains the modus operandi of ecological research today.

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Experiments are the way we do scientific research. Throughout this book, I will use the term “experiment” to refer to any kind of study that seeks to test a hypothesis. The term taken on its own is meant to encompass all types of experiments— whether in the field or the lab, whether observational (natural), manipulative or in silico. I will qualify experiment type when necessary and relevant for a particular example or issue. No matter what kind of experiment, or how simple or complex the question, good ecological research should strive to achieve all the elements of good experimental design. These are the use of controls, replication, and randomization. The complexity of ecological systems generally, and the spatial structure of landscapes specifically, mean that it can be challenging to meet the standards of these criteria to their fullest in all cases. Nonetheless, we should try to do so as best we can—as Koehnle and Schank (2009, p. 456) pointed out in their discussion about experimental controls: “… obtaining complete physical control in an ecological experiment may not be possible. Nonetheless, we also hold to the view that maximizing control is desirable” [emphasis in original]. This book is intended to help you to achieve that desire for good design as much as possible in landscape ecology experiments. We currently have more sophisticated tools at our disposal to measure the ecological world than Clements could ever have dreamt. Remote cameras, instruments that allow precision measurements of weather, soil and water chemistry, animal telemetry devices, GIS and remote sensing are all pieces of technology that enhance our ability to measure the natural world. Ecologists have also been great borrowers from other disciplines of science. We have adapted tools such as stable isotopes from chemists (e.g., Post, 2002) as a new lens at which to look at ecological questions around foraging, and DNA analysis from geneticists to look at populations in a different way (e.g., Sakai et al., 2001). At the same time, our ability to harness computational power to do ever-more complex statistical analysis and mathematical modelling has increased the sophistication of ecological experiments, as evidenced by the introduction of the journal Ecological Modelling in 1975. Nonetheless, ecologists should not completely abandon their natural history roots, as eloquently argued in an essay by Guidetti et  al. (2014). We will come back to this essay in Chap. 3, when we discuss experimentation within landscape ecology, since Guidetti et al. (2014) provocatively suggest that it is the “larger scale” branches of ecology, such as landscape ecology, that are most removed from natural history. In the next chapter, I will link Chaps. 1 and 2 to illustrate what the particular challenges to doing experiments are within a landscape ecology framework.

References Anwar, S., Khan, S. M., Ahmad, Z., et al. (2019). Floristic composition and ecological gradient analyses of the Liakot Forests in the Kalam region of District Swat, Pakistan. Journal of Forest Research, 30, 1407–1416. https://doi.org/10.1007/s11676-­019-­00919-­8

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Buma, B., Bisbing, S., Krapek, J., & Wright, G. (2017). A foundation of ecology rediscovered: 100 years of succession on the William S. Cooper plots in Glacier Bay, Alaska. Ecology, 98, 1513–1523. https://doi.org/10.1002/ecy.1848 Christie, A. P., Abecasis, D., Adjeroud, M., et al. (2020). Quantifying and addressing the prevalence and bias of study designs in the environmental and social sciences. Nature Communications, 11, 6377. https://doi.org/10.1038/s41467-­020-­20142-­y Clements, F. (1905). Research methods in ecology. University Publishing. Cooper, W. S. (1923a). The recent ecological history of Glacier Bay, Alaska: The interglacial forests of Glacier Bay. Ecology, 4, 93–128. https://doi.org/10.2307/1929485 Cooper, W. S. (1923b). The recent ecological history of Glacier Bay, Alaska: Permanent quadrats at Glacier Bay: An initial report upon a long-period study. Ecology, 4, 355–365. https://doi. org/10.2307/1929182 Cooper-Ellis, S., Foster, D. R., Carlton, G., & Lezberg, A. (1999). Forest response to catastrophic wind: Results from an experimental hurricane. Ecology, 80, 2683–2696. Cushman, S. A., Gutzweiler, K., Evans, J. S., & McGarigal, K. (2010). The gradient paradigm: A conceptual and analytical framework for landscape ecology. In S. Cushman & F. Heuttmann (Eds.), Spatial complexity, informatics, and wildlife conservation (pp. 83–108). Springer. Diamond, J. M. (1983). Ecology: Laboratory, field and natural experiments. Nature, 304, 586–587. https://doi.org/10.1038/304586a0 Diamond, J. (2001). Ecology: Dammed experiments! Science, 294, 1847–1848. https://doi. org/10.1126/science.1067012 Evans, J. S., & Cushman, S. A. (2009). Gradient modeling of conifer species using random forests. Landscape Ecology, 24, 673–683. https://doi.org/10.1007/s10980-­009-­9341-­0 Fajvan, M. A., Plotkin, A. B., & Foster, D. R. (2006). Modeling tree regeneration height growth after an experimental hurricane. Canadian Journal of Forest Research, 36, 2003–2014. https:// doi.org/10.1139/X06-­097 Gauch, H. G. J. (2003). Scientific method in practice. Cambridge University Press. Guidetti, P., Parravicini, V., Morri, C., & Bianchi, C. N. (2014). Against nature? Why ecologists should not diverge from natural history. Vie Milieu, 64, 1–8. Hairston, N. G., Sr. (1989). Ecological experiments: Purpose, design, and execution. Cambridge University Press. Hobbie, J.  E., & Likens, G.  E. (1973). Output of phosphorus, dissolved organic carbon, and fine particulate carbon from Hubbard Brook watersheds. Limnology and Oceanography, 18, 734–742. https://doi.org/10.4319/lo.1973.18.5.0734 Hurlbert, S. H. (1984). Pseudoreplication and the design of ecological field experiments. Ecological Monographs, 54, 187–211. Hurlbert, S.  H. (2009). The ancient black art and transdisciplinary extent of pseudoreplication. Journal of Comparative Psychology, 123, 434–443. https://doi.org/10.1037/a0016221 Jaeschke, A., Böhm, C., Merklinger, F.  F., et  al. (2019). Variation in δ15N of fog-dependent Tillandsia ecosystems reflect water availability across climate gradients in the hyperarid Atacama Desert. Global and Planetary Change, 183, 103029. https://doi.org/10.1016/j. gloplacha.2019.103029 Jongman, R. H. G., Ter Braak, C. J. F., & Van Tongeren, O. F. R. (Eds.). (1995). Data analysis in community and landscape ecology. Cambridge University Press. Karban, R., Huntzinger, M., & Pearse, I. S. (2014). How to do ecology: A concise handbook (2nd ed.). Princeton University Press. Kimmel, K., Dee, L. E., Avolio, M. L., & Ferraro, P. J. (2021). Causal assumptions and causal inference in ecological experiments. Trends in Ecology & Evolution. https://doi.org/10.1016/j. tree.2021.08.008 Koehnle, T. J., & Schank, J. C. (2009). An ancient black art. Journal of Comparative Psychology, 123, 452–458. https://doi.org/10.1037/a0017435 Kohler, R.  E. (2002). Labscapes and landscapes: Exploring the lab-field border in biology. University of Chicago Presss.

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Krebs, C. J. (1989). Ecological methodology. Harper Collins. Legendre, P. (1993). Spatial autocorrelation: Trouble or new paradigm? Ecology, 74, 1659–1673. https://doi.org/10.2307/1939924 Leigh, E. G., Jr., Wright, S. J., Herre, E. A., & Putz, F. E. (1993). The decline of tree diversity on newly isolated tropical islands: A test of a null hypothesis and some implications. Evolutionary Ecology, 7, 76–102. https://doi.org/10.1007/BF01237735 Liu, L., Wang, Y., Wang, Z., et al. (2019). Elevation-dependent decline in vegetation greening rate driven by increasing dryness based on three satellite NDVI datasets on the Tibetan Plateau. Ecological Indicators, 107, 105569. https://doi.org/10.1016/j.ecolind.2019.105569 McDonnell, M. J., & Hahs, A. K. (2008). The use of gradient analysis studies in advancing our understanding of the ecology of urbanizing landscapes: Current status and future directions. Landscape Ecology, 23, 1143–1155. https://doi.org/10.1007/s10980-­008-­9253-­4 Peet, R. K., & Loucks, O. L. (1977). A gradient analysis of southern Wisconsin forests. Ecology, 58, 485–499. Popper, K. (1963). Conjectures and refutations: The growth of scientific knowledge. Harper & Row. Post, D.  M. (2002). Using stable isotopes to estimate trophic position: Models, methods, and assumptions. Ecology, 83, 703–718. https://doi.org/10.1890/0012-­9658(2002)083[0703:USIT ET]2.0.CO;2 Resetarits, W. J., Jr., & Bernardo, J. (Eds.). (1998). Experimental ecology: Issues and perspectives. Oxford University Press. Sakai, A. K., Allendorf, F. W., Holt, J. S., et al. (2001). The population biology of invasive species. Annual Review of Ecology and Systematics, 32, 305–332. https://doi.org/10.1146/annurev. ecolsys.32.081501.114037 Schoener, T. W. (1982). The controversy over interspecific competition. American Scientist, 70, 586–595. Shreve, F. (1915). The vegetation of a desert mountain range as conditioned by climatic factors (Carnigie Institute Publication No. 127). Shreve, F. (1916). Experimental work at Cinchona. Science, 43, 919. Steel, R.  G. D., & Torrie, J.  H. (1980). Principles and procedures of statistics: A biometrical approach (2nd ed.). McGraw-Hill, Inc.. Steele, M. A. (1996). Effects of predators on reef fishes: Separating cage artifacts from effects of predation. Journal of Experimental Marine Biology and Ecology, 198, 249–267. https://doi. org/10.1016/0022-­0981(96)00011-­1 Terborgh, J., Lopez, L., Nuñez, P. V., et al. (2001). Ecological meltdown in predator-free forest fragments. Science, 294, 1923–1926. https://doi.org/10.1126/science.1064397 Urquhart, N. S. (1981). The anatomy of a study. HortScience, 16, 100–116. Whittaker, R. H. (1967). Gradient analysis of vegetation. Biological Reviews, 49, 207–264. Williams, B. K., & Brown, E. D. (2019). Sampling and analysis frameworks for inference in ecology. Methods in Ecology and Evolution, 10, 1832–1842.

Chapter 3

What Is It About Landscape Ecology That Makes Experimentation a Particular Challenge?

We cannot put a landscape into the lab, can we? – Tony. (“Tony” is one of the characters in Seppelt F, Müller F, Schröder B, Volk M. (2009) Challenges of simulating complex environmental systems at the landscape scale: a controversial dialogue between two cups of espresso. Ecological Modelling 220:3481–3489)

In Chap. 1, I introduced the field of landscape ecology, which fundamentally is concerned with linking ecological patterns and processes. Landscape ecology emphasizes spatially explicit analyses and we often carry out our research at large extents (tens to thousands of kilometres). In Chap. 2, I provided an overview of the history of experiments in ecology generally, and outlined the criteria for a good experiment (falsifiable hypotheses, statistical control, replication, and randomization). In this chapter, I will outline why combining experimentation, as described in Chap. 2, with landscape ecology, as described in Chap. 1, raises some challenges. I will also highlight what others have said about this topic and then outline how I will try to address these issues in the rest of this book. Before jumping into the challenges, let us review what I mean by an “experiment”. Here, as in Chap. 2, and throughout the book, we are considering both observational (“natural”) experiments and manipulative experiments. An observational experiment is one where the researcher lets some kind of natural process (e.g., a disturbance) be the experimental treatment, and samples in a way that facilitates making inferences about the impact of this process on one or more patterns or elements of the landscape. A manipulative experiment is one where the experimenter has explicit control of the experimental treatment, which can take place in either a lab or field setting or through an in silico simulation. In contrast, I am not considering a natural history study, in which we simply describe and classify our observations without any kind of treatment (natural or manipulated), to be experimental.

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3.1  Challenges with Experiments in Landscape Ecology The biggest challenge to doing experiments in landscape ecology is one of scale. Landscape ecology as a discipline evolved rapidly post World War II when aerial imaging became available to civilian researchers. This “bird’s eye view” of the world offered ecologists a new vantage point from which to examine how the natural world was organized. Later in the twentieth century, increased access to satellite imagery, and desktop computers capable of processing large data sets using remote sensing and GIS software, gave ecologists powerful new tools to analyse spatial patterns. The ability to have study areas ranging from hectares to hundreds of kilometers and the tools to study them are commonplace for landscape ecologists today. However, there is another consequence to our view from 10,000 feet up. In their essay “Against nature? Why ecologists should not diverge from natural history”, Guidetti et al. (2014) suggest that as the field of ecology broadly developed into more of an experimentally- and modelling-focused science (the latter is an apt characterization of the field of landscape ecology), the links to natural history observations fell away. They identified a tension between the role of experiments (of any kind) and natural history in ecological research. They suggest that early ecology focused on organisms (“autecology”), populations (“demoecology”) and communities and ecosystems (“synecology”) in natural settings which linked them more closely to natural history (Guidetti et  al., 2014). In contrast, the environmental issues of the latter half of the twentieth century moved ecology to larger spatial scales, with more integrative and applied work that led to the development of the subfields of macroecology, landscape ecology, and global ecology. Guidetti et al. (2014) argue that these “larger scale” ecologies are more disconnected from natural history, potentially to their detriment. The fact that we can do a landscape ecology study from our desks, using remotely sensed data and spatial modelling tools, means we do not need to set foot in the landscape under study. Guidetti et al. (2014) think this could be a problem, and they suggest that drawing on natural history may help ecologists to develop frameworks for hypotheses testing at larger scales. In a similarly thought-provoking essay, Dayton and Sala (2001) echo these sentiments. They propose that while hypothesis testing of theory is still fundamental to making ecology a scientific study, that some links to natural history will make us better scientists. They posit that “if ecologists embed this process in excellent natural history such that the tests are based in reality, we might recover the joy and spirit of natural history… while at the same time developing a better understanding of ecology” (Dayton & Sala, 2001, p. 203). Barrows et al. (2016) came to a similar conclusion in a survey of early-career professionals about their attitudes towards natural history—the majority felt that natural history was essential for field-based research, but felt that formal training was limited. Thus, it appears that our larger scale focus may be coming at the expense of being able to focus on the minutia of natural history. Issues of scale, which are fundamental to our discipline, introduce two specific challenges to doing experiments in landscape ecology. The first is that the focus at a large spatial extent forces us to confront the complexity of natural landscapes. The

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second is the difficulty of meeting the three criteria for good experimental design (control, randomization, and replication).

3.1.1  The Complexity of Natural Landscapes In their lament for the disconnect between natural history and some of the more recent sub-fields of ecology, Guidetti et al. (2014) argued that attempts to experiment in any ecological system are difficult. They point out that the simplified nature of many ecological experiments (e.g., as with mesocosms; see Chap. 8) are not representative of the complexity of real ecosystems, and that models may suggest mechanisms that may not apply well to the real world. On the other hand, they acknowledge that a natural history approach (as described in the previous chapter), which does appreciate the complexity of ecological systems, may be confounded by too many variables to allow for experimentation. In reference to landscape and macroecology, Guidetti et al. (2014) suggest that natural history observations may actually play a key role, despite the disconnect that they accuse “large scale” ecologists of having with the natural world from their computers. However, given that the scale of such studies makes them less amenable to experimentation, perhaps a focus on natural history could be helpful. They cite space-for-time comparisons (an example of which is Cooper’s Glacier Bay studies discussed in the previous chapter) as a type of study (although Guidetti et al. (2014) reference these as “not properly experimental”) that benefits from close observations of the natural world. They conclude that “(n)atural history, in the context of ecological studies, is crucial to provide a proper background in which realistic scenarios can be envisaged and meaningful hypotheses be constructed, relevant variables selected and pertinent questions answered” (Guidetti et  al., 2014, p.  6). Thus, there is a tension between natural-­ history focused approaches to research vs. empirically driven modelling approaches. The underlying complexity of the landscape will always be there—and neither approach to trying to understand it is right or wrong. Ultimately, the choice of where to adopt a descriptive, natural history approach, or an empirical modelling one is influenced by any combination of the research question, the skills or budget of the research team, and the logistics of the study. However, we must be careful not to label solely descriptive work as experimental. While the complexity of landscapes may make it seem difficult to experiment, this complexity, in terms of spatial pattern and hierarchical structure has been widely acknowledged, and indeed, embraced, in our discipline (Turner, 1987; Urban et al., 1987; Turner, 1989; Cushman et al., 2010). For example, much of the early landscape ecology work in Europe was about describing and classifying geographical variation in landforms and landcover (e.g., Watt, 1947; Solnetsev, 1948; Troll, 1950). However, the ecological study of landscapes is also complex given that the discipline itself is interdisciplinary (Tress et al., 2005). Landscape ecology combines aspects of biological (ecology, wildlife biology, plant science) physical (geography, geology, soil science) and social (economics, policy, planning) sciences

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(Risser 1987). Thus, a nuanced understanding of landscape patterns and processes will require some cross-disciplinary understanding. Conducting experiments within landscapes will take a careful approach, due in part to the inherent complexity of landscapes, but also to particular challenges of experimental design, as discussed below.

3.1.2  Experimental Design Challenges – Replication In landscape ecology studies, which are often at the extent of tens to hundreds or even thousands of kilometres, it can be challenging to carry out experiments because of the difficulty in replicating the treatments. Despite that replication is a key element for statistical hypothesis testing and analysis (see Chap. 2) some of the most influential (and highly cited) papers in the journal Landscape Ecology have little to no replication. In the Editor-in-Chief’s retrospective piece on the 30th anniversary of the journal, Wu (2017) highlighted the development and growth of the journal, and the field of landscape ecology, by listing the top 30 papers cited in the journal since its inception (Table 1 in Wu, 2017). Only half of these papers were empirical work (the rest were reviews, methods papers, or used simulated data). Two papers documented what we could consider “true replicate” landscapes; only one of which was a study done at a ‘typical’ kilometres-extent landscape. The other paper with replicate landscapes had 10 artificially-constructed landscapes which were used to test the effect of landscape pattern and scaling on beetle movement (Wiens & Milne, 1989). Only a observational experiment in the Netherlands (van Dorp & Opdam, 1987) had an impressive sample size of 235 replicate woodlots (average size 9.65 ha) embedded in an altered landscape. Since early landscape ecologists did not necessarily always publish in Landscape Ecology, it is useful to examine other journal content from this era as well. Influential early landscape ecology papers published in other journals often describe concepts in the discipline to a broader readership (e.g., Merriam, 1988; Turner, 1989; Kotliar & Wiens, 1990; McDonnell & Pickett, 1990). Early and influential empirical studies published outside of Landscape Ecology touched on key concepts such as disturbance (e.g., Turner et al., 1989a), networks (e.g., Forman & Baudry, 1984) and applications to conservation issues (e.g., Baker, 1989). Experimental approaches included computer simulation models (Turner et al., 1989a), and descriptive approaches (Forman & Baudry, 1984; Baker, 1989), however without replication. Many of the early empirical papers in Landscape Ecology and elsewhere focused on exploring and quantifying patterns and investigating how different metrics performed at different scales and how they related to each other (Wu, 2017). These often used multiple landscapes in the analysis, but often these were chosen to be contrasting to examine the patterns between and across different types of landscapes (e.g., Franklin & Forman, 1987; Turner et al., 1989b). One paper used replicates within a factor analysis to try to generate a better understanding of how metrics related (Riitters et  al., 2002) and another did a similar analysis to test for

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correlations (O’Neill et al., 1988). Thus, in the first 30 years of landscape ecology, at least as represented in the flagship journal, few papers had experimental replicates, owing in part to the fact that the discipline was in early stages of development, coupled with the challenges of experimenting with kilometres-extent landscapes. More recent top papers in Landscape Ecology (the top 30 between 2006–2016; Table 2 in Wu, 2017) show little development towards the use of experimental replicates. Six of these are “Perspectives” pieces, and nine are reviews, editorials, notes, or concept papers, perhaps reflecting some stock-taking of the discipline in its second and third decades. We can see evidence of how the field developed because this top-30 list includes one meta-analysis and four papers that use simulation models. Of the remaining ten papers, five are studies within a single landscape; two papers analyse multiple landscapes, but not experimentally. One analyses multiple wetlands, but for comparative purposes (Mitsch et al., 2013) and another looks at the contribution of domestic gardens to urban green spaces across five cities (Loram et al., 2007). Only 3 of the top 30 papers cited in Landscape Ecology from 2006 to 2016 have true experimental replicates: Schulte et al. (2007), Concepción et al. (2008) and Smith et al. (2009). This leads to the question of whether replication is possible in most landscape ecology experiments. If replication is not feasible, then the question is whether experiments in the field in landscape ecology simply have to do so without the benefit of replication most of the time. If that is the case, then what are the implications for the discipline as a scientific endeavour? Are there considerations and strategies for experiments at landscape extents that will still allow robust experimentation? What are ways that scientists have overcome the logistical challenges of doing experiments across broad extents of landscapes? I hope to answer these questions with this book.

3.1.3  Experimental Design Challenges – Randomization In Chap. 2, I discussed how randomization is a critical attribute for good experimental designs as a means to avoid consciously or inadvertently biasing the data. However, even if we accept that a landscape ecology experiment can have an n of 1 (i.e., be carried out in a single landscape), randomizing data collection can be challenging. This is because landscapes have inherent spatial pattern, resulting in the phenomenon of points in a landscape that are closer together being inherently more similar to each other than points further away (known as Tobler’s first law of Geography; Tobler, 1970 as cited in Miller, 2004). Some landscapes have patterns that are highly structured (think of the regular spacing of plants in arid environments; e.g., Roberts & Jones, 2000), while others have patterns that repeat across larger extents (imagine vegetation changes along parallel ridges of hillslopes

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running east-west or patterns as described in Vincenot et al., 2016).1 In a landscape of parallel ridges, we would expect certain patterns on each south-facing slope to repeat, and patterns in peaks and valleys to repeat at intervals coincident with the high and low elevation points. Thus, how samples are spaced has very important implications for assumptions about data independence. I will address the issue of spatial autocorrelation (and the tangential issue of pseudoreplication) in detail in the next chapter.

3.1.4  Experimental Design Challenges – Controls As outlined in Chap. 2, true experimental controls (i.e., conditions identical in all factors except for the treatment of interest) are difficult in any ecological study. The challenge of applying a control in a landscape-scale experiment is due largely to the size and complexity of landscapes. The lack of ability to replicate (see above) means that to even have one replicate as a control can be difficult to implement! To confound things further, in landscape ecology, we often exploit spatial variation explicitly, while in other field ecology studies, space is explicitly “controlled for” (Resetarits & Bernardo, 1998). Thus, the clever scientist needs to determine how they are making use of the landscape in which they are doing their experiment. Is it merely the “stage” on which the “actors” of the experiment are playing (Hutchinson, 1965)? In that case, it is spatial variation that we need to control for. If we are interested in seeing how the actors respond to variation across the stage, then spatial variation becomes the experimental variable that the researcher seeks to manipulate or sample directly.

3.1.5  Experimental Design Challenges – Validity A further challenge with experimental design is the degree of internal and external experimental validity. Internal experimental validity refers to how much of the experimental results are attributed to the factor being manipulated rather than some unknown and unmeasured effect, while external validity assesses how much the experimental results can be generalized to a wider population or landscape (Naeem, 2001). Figure  3.1 illustrates how different types of experiments mean trade-offs between internal and external validity. I have adapted this figure from Naeem (2001) with labels that correspond to the chapters in the second half of this book.

1  The review paper by Rietkerk and van de Koppel (2008) includes some striking images of spatial patterns as well as a link to a Google Earth tour of sites around the globe which display regular patterns.

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Fig. 3.1  The effect of experimental type on internal vs. external experimental validity, and the relationship to theory (from which deductive hypotheses originate) and observation (from which inductive hypothesis originate). Experiments with high internal validity will better validate theory, and those with high external validity will better validate patterns observed in nature. The different experimental types discussed in the subsequent chapters of this book are indicated in the box at the bottom and all along a spatial continuum from small to large extent. (Figure adapted with permission from Naeem (2001))

3.2  A  ddressing Challenges of Experimentation in Landscape Ecology In a 2012 paper on experimental landscape ecology, Jenerette and Shen (2012) reviewed a suite of papers to see how researchers have addressed these challenges. They outlined 15 different types of experiments in landscape ecology, which they grouped by overall research objective. These objectives were: (1) identification of landscape structure; (2) identification of process variation within landscapes; (3) identification of process sensitivity to landscape structure; and (4) identification of landscape pattern formation factors. Their taxonomy of experimental types linked to objectives is extremely useful (Table 3.1), and their paper provided brief examples of each type. My goal here is to provide specific detail on how to do different types of experiments in landscape ecology, along with tangible resources. Throughout this book, I will link the different experimental approaches described here to the taxonomy and objectives of experiments as described by Jenerette and Shen (2012). Thus, if you are not familiar with their paper, you may want to read it before you delve further into this book! Jenerette and Shen (2012) also identified that landscape experiments inherently carry some trade-offs, such as challenge of scaling in real landscapes vs. generalizing across landscapes; between classical statistical analysis vs. flexible designs; or between complexity and resource requirements. Throughout the various chapters of this book, I will try to highlight these trade-offs in detail, so that landscape

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Table 3.1  Taxonomy of landscape ecology experiments as developed by Jenerette and Shen (2012). See Table 1 in their paper for example papers of each of the 15 types of experiments Group I. Identification of landscape structure II. Identification of process variation within landscapes

III. Identification of process sensitivity to landscape structure

IV. Identification of landscape pattern formation factors

Type 1. Perception experiments 2. Tracer experiments 3. In situ experiments distributed throughout an experiment 4. Ex situ experiments using samples collected throughout a landscape 5. Translocation experiments 6. Transport manipulations 7. Manipulation of internal patch characteristics 8. Manipulations of patch shape 9. Manipulation of patch connectivity 10. Fragmentation experiments 11. Manipulation of landscape scale 12. Construction of entire landscapes 13. Manipulate disturbances 14. Vector manipulation 15. Self-organization experiments

ecologists can best assess what type of experiment is most useful for their particular research question. As highlighted already in this chapter, and the previous one, ecologists have generally made hard distinctions between manipulative and observational experiments. Tensions have existed since the beginning of ecology as a science between those who value observational vs. manipulative studies (Kohler, 2002), although whether these tensions are necessary is open for debate (Diamond, 2001). The tension arises largely because of one of the trade-offs observed by Jenerette and Shen (2012) and others (Diamond, 1983); that between realism and feasibility. A useful approach suggested for understanding large, complex landscapes has been through observational studies. Such studies can be feasible and realistic. For example, von Gadow et al. (2016) provided an overview of the Bavarian Forest Research Institute’s extensive database of individual trees, sampled across 1200  ha of field plots and which have had detailed measurements taken over time, some since as early as 1870. They illustrate how recent manipulative experiments (e.g., experimental plantings to assess impacts on carbon-sequestration) also benefit from being conducted in forests with such long-term data sets, as it facilitates model parametrization and extrapolation of inferences from the manipulative experiment to larger extents in space and time. They identify similar datasets in other forest systems around the world as well as the potential for cross-sectional (‘space-for-time’ substitutions) analyses to provide similar extensive data for either manipulative or observational experiments (von Gadow et al., 2016). Some have called observational studies ‘quasi-experiments’ (Butsic, et al. 2017; Larsen et al., 2019); likely in an effort to distinguish them from lab- or field-based

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manipulations. As Butsic et al. (2017) point out, other disciplines, such as economics, have developed entirely using quasi-experiments, and in Chap. 2, I emphasized that we are considering observational experiments to be unequivocally considered as experiments. This does not mean that observational experiments do not have unique characteristics that require consideration. For example, it may be more difficult for a researcher to implement an experimental control in an observational experiment than in a manipulative one. It may be more difficult to have full replication of all experimental units in an observational experiment, because of the underlying spatial pattern. Attention to underlying pattern will be necessary, and adjustments to sampling design may be necessary to increase statistical rigour (e.g., stratified random or block designs). Butsic et al. (2017) provide a detailed overview of how ecologists can borrow statistical tools from economists to analyse quasi-­ experimental data. A key in robust statistical analysis is the partitioning of data into ‘control’ and ‘treatment’ groups. In an observational experiment, this can be done through matching estimators, discontinuity design, difference-in-difference models, or with instrumental variables. I highlight their paper in the Resources section at the back of the book, as it provides sample data and code to allow researchers to apply these statistical tools to their own “quasi-experiments”.

3.3  The Bottom Line As the discipline of landscape ecology has grown and developed over the last ~30 years, the field has grappled with how it “does science” at landscape extents, an issue noted earlier by Hobbs (1999). Few of the seminal papers in the field have been able to do manipulative experiments. This is still posited as a good standard to aim for when possible (Wiens et al., 2006; Jenerette & Shen, 2012), though consensus within landscape ecology (at least based on an evaluation of papers that have made it through peer review in the flagship journal) is that observational experiments are acceptable in many cases. As well, not all landscape studies need to be explicitly experimental (Wiens, 1999). Impact studies, for example, are a type of empirical research that need not necessarily follow the rigorous standards of experimental design (Larsen et al., 2019). The explicit focus that landscape ecology has on heterogeneity, dynamics and linking patterns and processes across scales will always benefit from studies that happen in the real world, and the majority of these are, and will continue to be, observational experiments. Studies in the real world and at large extents will face challenges in doing manipulative experiments. We have learned a great deal from observational experiments in landscape ecology to date, and I do not intend for this book to be a critique of such studies. Rather, I hope to use this book as a way for the next generation of landscape ecologists to think about how they might add more and different kinds of experimentation to their toolkit, and to think about ways to increase their ability to evaluate rigorously hypotheses within observational studies. To do the latter, landscape ecologists need to carefully consider sampling design (including replication and pseudoreplication

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along with the challenges of spatial autocorrelation), along with issues of scale. I discuss these issues in depth in Chaps. 4 and 5. Part II of the book offers individual chapters that describe and dissect different approaches to doing experiments in landscape ecology, illustrated with many examples. These include experiments at the large landscape extent, which may be manipulative (Chap. 6) or make use of experimental model landscapes (Chap. 7). I also discuss experiments that move away from realism and into more highly controlled environments, such as mesocosms in Chap. 8 and microcosms in Chap. 9. Finally, in the last two chapters of Part II, I discuss novel approaches to do landscape ecology in systems that may not be considered ‘landscapes’ by some, including in silico studies (Chap. 10) and novel landscapes (Chap. 11).

References Baker, W. L. (1989). Landscape ecology and nature reserve design in the Boundary Waters Canoe Area, Minnesota. Ecology, 70, 23–35. Barrows, C. W., Murphy-Mariscal, M. L., & Hernandez, R. R. (2016). At a crossroads: The nature of natural history in the twenty-first century. BioScience, 66, 592–599. https://doi.org/10.1093/ biosci/biw043 Butsic, V., Lewis, D. J., Radeloff, V. C., et al. (2017). Quasi-experimental methods enable stronger inferences from observational data in ecology. Basic and Applied Ecology, 19, 1–10. https:// doi.org/10.1016/j.baae.2017.01.005 Concepción, E. D., Díaz, M., & Baquero, R. A. (2008). Effects of landscape complexity on the ecological effectiveness of agri-environment schemes. Landscape Ecology, 23, 135–148. https://doi.org/10.1007/s10980-­007-­9150-­2 Cushman, S. A., Gutzweiler, K., Evans, J. S., & McGarigal, K. (2010). The gradient paradigm: A conceptual and analytical framework for landscape ecology. In S. Cushman & F. Heuttmann (Eds.), Spatial complexity, informatics, and wildlife conservation (pp. 83–108). Dayton, P. K., & Sala, E. (2001). Natural history: The sense of wonder, creativity and progress in ecology. Scientia Marina, 65, 199–206. https://doi.org/10.3989/scimar.2001.65s2199 Diamond, J. (2001). Ecology: Dammed experiments! Science, 294, 1847–1848. https://doi. org/10.1126/science.1067012 Diamond, J. M. (1983). Ecology: Laboratory, field and natural experiments. Nature, 304, 586–587. https://doi.org/10.1038/304586a0 Forman, R. T. T., & Baudry, J. (1984). Hedgerows and hedgerow networks in landscape ecology. Environmental Management, 8, 495–510. Franklin, J.  F., & Forman, R.  T. T. (1987). Creating landscape patterns by forest cutting: Ecological consequences and principles. Landscape Ecology, 1, 5–18. https://doi.org/10.1007/ BF02275261 Guidetti, P., Parravicini, V., Morri, C., & Bianchi, C. N. (2014). Against nature? Why ecologists should not diverge from natural history. Vie Milieu, 64, 1–8. Hobbs, R. J. (1999). Clark Kent or Superman: Where is the phone booth for landscape ecology? In J. M. Klopatek & R. H. Gardner (Eds.), Landscape ecological analysis (pp. 11–23). Springer. Hutchinson, G. E. (1965). The ecological theatre and the evolutionary play. Yale University Press. Jenerette, G.  D., & Shen, W. (2012). Experimental landscape ecology. Landscape Ecology, 27, 1237–1248. https://doi.org/10.1007/s10980-­012-­9797-­1 Kohler, R.  E. (2002). Labscapes and landscapes: Exploring the lab-field border in biology. University of Chicago Press.

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Kotliear, N. B., & Wiens, J. A. (1990). Multiple scales of patchiness and patch structure: A hierarchical framework for the study of heterogeneity. Oikos, 59, 253–260. Larsen, A. E., Meng, K., & Kendall, B. E. (2019). Causal analysis in control–impact ecological studies with observational data. Methods in Ecology and Evolution, 10, 924–934. https://doi. org/10.1111/2041-­210X.13190 Loram, A., Tratalos, J., Warren, P. H., & Gaston, K. J. (2007). Urban domestic gardens (X): The extent & structure of the resource in five major cities. Landscape Ecology, 22, 601–615. https:// doi.org/10.1007/s10980-­006-­9051-­9 McDonnell, M. J., & Pickett, S. T. A. (1990). Ecosystem structure and function along urban-rural gradients: An unexploited opportunity for ecology. Ecology, 71, 1232–1237. Merriam, G. (1988). Landscape dynamics in farmland. Trends in Ecology & Evolution, 3, 16–20. Miller, H. J. (2004). Tobler’s first law and spatial analysis. Annals of the Association of American Geographers, 94, 284–289. Mitsch, W.  J., Bernal, B., Nahlik, A.  M., et  al. (2013). Wetlands, carbon, and climate change. Landscape Ecology, 28, 583–597. https://doi.org/10.1007/s10980-­012-­9758-­8 Naeem, S. (2001). Experimental validity and ecological scale as criteria for evaluating research programs. In R. H. Gardner, W. M. Kemp, V. S. Kennedy, & J. E. Petersen (Eds.), Scaling relations in experimental ecology (pp. 223–250). Columbia University Press. O’Neill, R.  V., Krummel, J.  R., Gardner, R.  H., et  al. (1988). Indices of landscape pattern. Landscape Ecology, 1, 153–162. https://doi.org/10.1007/BF00162741 Resetarits, W. J., Jr., & Bernardo, J. (Eds.). (1998). Experimental ecology: Issues and perspectives. Oxford University Press. Rietkerk, M., & van de Koppel, J. (2008). Regular pattern formation in real ecosystems. Trends in Ecology & Evolution, 23, 169–175. https://doi.org/10.1016/j.tree.2007.10.013 Riitters, K. H., O’Neill, R. V., Hunsaker, C. T., et al. (2002). A factor analysis of landscape pattern and structure metrics. Landscape Ecology, 17, 23–39. https://doi.org/10.1007/BF00158551 Risser, P. G. (1987). Landscape ecology: State of the art. In M. G. Turner (Ed.), Landscape heterogeneity and disturbance (pp. 3–14). Springer. Roberts, C., & Jones, J.  A. (2000). Soil patchiness in juniper-sagebrush-grass communities of Central Oregon. Plant and Soil, 223, 47–61. https://doi.org/10.1023/A:1004745329332 Schulte, L. A., Mladenoff, D. J., Crow, T. R., et al. (2007). Homogenization of northern U.S. Great Lakes forests due to land use. Landscape Ecology, 22, 1089–1103. https://doi.org/10.1007/ s10980-­007-­9095-­5 Smith, A. C., Koper, N., Francis, C. M., & Fahrig, L. (2009). Confronting collinearity: Comparing methods for disentangling the effects of habitat loss and fragmentation. Landscape Ecology, 1271. https://doi.org/10.1007/s10980-­009-­9383-­3 Solnetsev, N. A. (1948). The natural geographic landscape and some of its general rules (translated by Khoroshev AV, Andronikov S). In J. A. Wiens, M. A. Moss, M. G. Turner, & D. J. Mladenoff (Eds.), Foundation papers in landscape ecology (pp. 19–27). Columbia University Press. Tress, G., Tress, B., & Fry, G. (2005). Clarifying integrative research concepts in landscape ecology. Landscape Ecology, 20, 479–493. https://doi.org/10.1007/s10980-­004-­3290-­4 Troll, C. (1950). The geographic landscape and its investigations (translated by Davidsen C). In J. A. Wiens, M. A. Moss, M. G. Turner, & D. J. Mladenoff (Eds.), Foundation papers in landscape ecology (pp. 71–101). Columbia University Press. Turner, M. G. (1989). Landscape ecology: The effect of pattern on process. Annual Review of Ecology and Systematics, 20(20), 171–197. https://doi.org/10.1146/annurev.es.20.110189.001131 Turner, M. G. (Ed.). (1987). Landscape heterogeneity and disturbance. Springer. Turner, M. C., Gardner, R. H., Dale, V. H., & O’Neill, R. V. (1989a). Predicting the spread of disturbance across heterogeneous landscapes. Oikos, 55, 121–129. Turner, M. G., O’Neill, R. V., Gardner, R. H., & Milne, B. T. (1989b). Effects of changing spatial scale on the analysis of landscape pattern. Landscape Ecology, 3, 153–162. https://doi. org/10.1007/BF00131534

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Urban, D. L., O’Neill, R. V., & Shugart, H. H. (1987). Landscape ecology: A hierarchical perspective can help scientists understand spatial patterns. Landscape Ecology, 37, 119–127. van Dorp, D., & Opdam, P. F. M. (1987). Effects of patch size, isolation and regional abundance on forest bird communities. Landscape Ecology, 1, 59–73. https://doi.org/10.1007/BF02275266 Vincenot, C. E., Carteni, F., Mazzoleni, S., et al. (2016). Spatial self-organization of vegetation subject to climatic stress—insights from a system dynamics—individual-based hybrid model. Frontiers in Plant Science, 7, 636. von Gadow, K., Zhao, X. H., Tewari, V. P., et al. (2016). Forest observational studies: An alternative to designed experiments. European Journal of Forest Research, 135, 417–431. https://doi. org/10.1007/s10342-­016-­0952-­0 Watt, A.  S. (1947). Pattern and process in the plant community. In J.  A. Wiens, M.  A. Moss, M. G. Turner, & D. J. Mladenoff (Eds.), Foundation papers in landscape ecology (pp. 102–124). Columbia University Press. Wiens, J.  A. (1999). The science and practice of landscape ecology. In J.  M. Klopatek & R. H. Gardner (Eds.), Landscape ecological analysis (pp. 371–383). Springer. Wiens, J. A., & Milne, B. T. (1989). Scaling of “landscapes” in landscape ecology, or, landscape ecology from a beetle’s perspective. Landscape Ecology, 3, 87–96. https://doi.org/10.1007/ BF00131172 Wiens, J. A., Stenseth, N. C., Van, H. B., & Ims, R. A. (2006). Ecological mechanisms and landscape ecology. Oikos, 66, 369–380. https://doi.org/10.2307/3544931 Wu, J. (2017). Thirty years of landscape ecology (1987–2017): Retrospects and prospects. Landscape Ecology, 32, 2225–2239. https://doi.org/10.1007/s10980-­017-­0594-­8

Chapter 4

Replication vs. Pseudoreplication: Are We Making Too Big a Deal of This?

Pseudoreplication should not be the death knell it has become for scientific papers G. Matt Davies and Alan Grey (from: Davies GM, Gray A. (2015) Don’t let spurious accusations of pseudoreplication limit our ability to learn from natural experiments (and other messy kinds of ecological monitoring). Ecol Evol 5: 5295–5304)

4.1  Introduction The discipline of landscape ecology is concerned with how spatial patterns influence ecological processes and vice versa (Wu & Hobbs, 2002; Turner, 2005; Li & Mander, 2009). As discussed in the previous chapter, the spatial scale at which many  of these types of research are conducted make it challenging to conduct manipulative experiments (Wiens & Milne, 1989; Ims, 2005) and to sufficiently replicate analyses to enable robust hypothesis testing (Wiens & Milne, 1989; Hargrove & Pickering, 1992). It is not uncommon to see landscape ecology studies that are observational experiments with one “treatment” and one “control” landscape, each of which may be kilometres in extent. Many of these compare landscape-­ scale patterns and/or processes across two landscapes that differ in some way—often by disturbance type or management regime (e.g., Mladenoff et al., 1993; Schulte et al., 2007; Zlonis & Niemi, 2014; Boucher et al., 2015, 2017; LeClerc & Wiersma, 2017; Zong et al., 2018). However, in such a study design, the researcher has insufficient replication of the experimental unit (i.e., the landscape) to allow for statistical analysis. One way to enable statistical testing is to compare subsamples within each of the two experimental units. A researcher can efficiently sample smaller sample plots within the treatment/control landscapes, giving sufficient replication of sample plots to do statistical testing. This is a very common strategy (e.g., Renjifo, 2001; Fletcher & Hutto, 2008). However, Stuart Hurlbert (1984, 2009) would accuse such a study design of being pseudoreplicated. The issue of © Springer Nature Switzerland AG 2022 Y. F. Wiersma, Experimental Landscape Ecology, Landscape Series 29, https://doi.org/10.1007/978-3-030-95189-4_4

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pseudoreplication (what has been called the “doctrine of pseudoreplication”; Schank & Koehnle, 2009) has been described as “genuine and controversial” (Davies & Gray, 2015). It is largely the result of a misunderstanding of the issue, coupled with a copious (and sometimes densely written) series of back-and-forth arguments between sides in various streams of literature (Hargrove & Pickering, 1992; Schank, 2001; van Mantgem et al., 2001; Oksanen, 2001, 2004; Cottenie & De Meester, 2003; Millar & Anderson, 2004; Bataineh et  al., 2006; Schank & Koehnle, 2009; Freeberg & Lucas, 2009; Koehnle & Schank, 2009; Nikinmaa et al., 2012; Ramage et al., 2013; Davies & Gray, 2015; Spurgeon, 2019). My intent with this chapter is to clarify what pseudoreplication—as described by Hurlbert (1984, 2009)—is and to identify what the key misunderstandings, issues, and debates are about whether and how much it matters. I will also offer suggestions specific to landscape ecology about how to design experiments to avoid charges of pseudoreplication. Stuart Hurlbert, a biologist at San Diego State University with research interests in the limnology of saline lakes, wrote a paper in 1984 that introduced the term of pseudoreplication to field biologists. This paper has been hugely influential; Google Scholar lists over 8800 citations as of mid-2020, and in 1984, the American Statistical Association awarded it the G.W. Snedecor Award for the Best Publication in Biometry. The Ecological Society of America listed it as one of the notable papers in ESA history in the Centennial Special issue of Ecological Monographs in June 2016. Hurlbert’s 1984 paper is dated, yet continues to be debated and discussed. While there is no doubt that iconoclasts like Hurlbert can have a major influence on how we do science, I must make note of the fact that Hurlbert has made use of his privileged position within a university to disseminate racist and anti-immigrant screeds (Flaherty, 2002; Kloor, 2018). Despite the fact that his writing is persuasive, this fact makes him anything-but-heroic in my view. Nonetheless, instead of dismissing his work outright because his political views are toxic, I propose to dissect the issue of pseudoreplication to show that knee-jerk dismissal of studies because they appear to be pseudoreplicated (as documented by Davies & Gray, 2015) are problematic, just as is knee-jerk characterization of groups of people as criminals based on their country of origin. Additionally, I hope to show that much of what Hurlbert’s papers have propagated over the years can be solved with some careful thought to experimental design and statistical analysis. So what is the big deal with pseudoreplication? What exactly is pseudoreplication?

4.2  What Is Pseudoreplication? Pseudoreplication is a term that applies to the design of experimental studies and the implications this has on statistical inference. Hurlbert (1984, p. 190) defined pseudoreplication as “the testing for treatment effects with an error term inappropriate to the hypothesis being considered”. The issue here (but not explicitly stated by Hurlbert, 1984) is the need for clarity about the limits of the inference; that is,

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whether one is making a hypothesis about the patterns within the particular system or location they are sampling, or whether one is trying to make inferences beyond the data that are sampled. Another confounding issue (not discussed in Hurlbert, 1984) is whether the effects under investigation are fixed effects or random effects. I will come back to these two ideas (about limits to inference and fixed vs. random effects) in a moment. However, the discussion of pseudoreplication gets muddy, because Hurlbert (1984, p. 190) goes on to describe pseudoreplication as “… experimental design (or sampling) and statistical analysis which is inappropriate for the hypothesis of interest”. Thus on the one hand, pseudoreplication is defined as a problem with how error is allocated in calculating the F-ratio (the first definition, above), and on the other hand, it is a term to describe a mismatch of statistical analysis and experimental design (the latter description). Later, Hurlbert (1984, p. 198) describes pseudoreplication happening when one has experimental designs where treatments are “spatially or temporally segregated… if all replicates of a treatment are somehow interconnected,… or if ‘replicates’ are only samples of a single experimental unit”. This is a slightly different thing again, so it is no wonder that there is confusion over what pseudoreplication is, or when it has been committed. A further way in which Hurlbert (1984) describes how pseudoreplication can occur might raise red flags for landscape ecologists (whose work is nearly always concerned with space), when he states that pseudoreplication is “often a consequence of the actual physical space over which samples are taken or measurements made being smaller or more restricted than the inference space implicit in the hypothesis being tested” (Hurlbert, 1984, p. 190). He gives an example of placing 8 litter bags at two sites, which are at two different depths in a lake, as an example of pseudoreplication. This is because one cannot assume any difference between the two sets of 8 bags is due to the difference in the depths at which the bags were deployed (the ecological hypothesis) or whether it is simply by random chance of the two locations being different in some other, unknown way. The idea that differences in spatial location might drive differences in ecological patterns and/or processes is at the crux of what landscape ecologists study. In our discipline, we treat space explicitly, whereas Hurlbert (1984) is concerned about when space is implicit. Thus, in the litter bag example, there is nothing inherently wrong with placing 8 litter bags at one single location on the 1-m isobath and 8 on the 10-m isobath, so long as the researcher realizes that the inferences they draw from the analysis apply only to those particular locations in that particular lake and that their experimental design does not allow them to reliably infer how decomposition varies at 1 m vs. 10 m depth in general terms for a broader suite of lakes (or even other locations within the same lake that was sampled). Understanding the difference between spatially-­implicit vs. spatially-explicit approaches to experimental design is critical for ensuring experiments are statistically robust as well as understanding the limits of inference. A study where space is treated explicitly will usually be limited to making inferences within that system, while a study where space is treated implicitly may—if designed and analysed correctly—be more amenable to inferences beyond the study system.

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In a more detailed discussion of pseudoreplication, Hurlbert (2009) elaborates on how it applies to manipulative experiments (but did not treat observational experiments in more detail, for reasons which may become obvious as you read this chapter). He refines his definition of pseudoreplication here (the 2009 paper is largely a rebuttal to Schank & Koehnle, 2009 who referred to pseudoreplicaton as a “pseudoproblem”) as “a single experiment unit per treatment, but multiple measurements on each experimental unit… These multiple measurements are then treated statistically as if each represented a separate experimental unit” (Hurlbert, 2009, p. 437, ellipses as in original). Other examples of pseudoreplication that have been given for manipulative experiments are treating the individuals housed within cages, tanks or aquaria as replicates, when in fact the cages, tanks, or aquaria are the replicates (Hurlbert, 1984, 2009). Although the clarity of definitions of the terms experiment, experimental unit and evaluation unit in the latter paper (Hurlbert, 2009) are useful, two key terms which are not defined, but which are highly germane to the issue at hand, are those of fixed effects and random effects. Fixed effects are those factors that are of interest to the researcher (for example, we might want to know how four different levels of fertilizer treatment affect plant growth). Fixed effects are the thing we measure or manipulate, and which we would use again if repeating the experiment (Quinn & Keough, 2002). Random effects are those elements of our sample that are a random subset of all possible levels or groups. For example, in a fertilizer experiment, those plants we select for our different experimental treatments are a random selection of all the individuals of that species available to us. Random effects are the thing we want to make an inference about—if we see that fertilizer level B has the best outcome for plant growth, we infer that will be true for all plants of that species, not just the individuals we experimented on. To verify this, we might run the experiment again, with a different random sample of plants. I provide some additional definitions and discussion of the terms “fixed effect” and “random effect” in the glossary. It is important to note that there are not hard and fast rules about when an effect is fixed or random. Often, the decision depends on what the intent of the investigation is, as well as the investigator’s judgement of the system (Eisenhart, 1947; Quinn & Keough, 2002; Stroup, 2013; Lawson, 2015).

4.2.1  Expected Mean Squares and F-Ratios I will walk through some examples of experimental design and statistical analysis (including decisions about which elements of the design to designate as fixed or random effects) using a statistical test that is likely familiar to most readers—the Analysis of Variance (ANOVA). An ANOVA uses an F-ratio to test whether there is a statistically significant difference between the treatment and control samples that is not due to random chance. To illustrate how one could delineate fixed and random effects in an ANOVA, imagine a study where a landscape ecologist is looking at the effect of time since

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fire on groundcover diversity. The ecologist randomly chooses 20 sample sites within 3 different forest stands (tens to hundreds of hectares) that are generally similar in all respects (e.g., climate, soil, dominant tree species) but vary in the time since the last fire. At each of the 20 sites, the ecologist uses a point-quarter sampling technique with four 1 m × 1 m quadrats at which they measure groundcover diversity (see Fig. 4.1a). This type of study design where some kind of biological diversity metric is compared across two or more locations with different times-since-disturbance is not atypical in landscape ecology (e.g., Taillie et  al., 2018; Adedoja et al., 2019; Mahood & Balch, 2019) and echoes the space-for-time designs described in Chap. 2. In the imagined case described here, the number of levels of the treatment (of time since fire) is by stand (a = 3), with only one replicate of each (i.e., they do not have multiple stands which have 10, 50 or 100 years since fire available to sample). If the ecologist treated the sample sites per stand as the experimental replicates in their statistical anlaysis, they would likely face accusations of pseudoreplication (Davies & Gray, 2015). A more appropriate way to handle the data in this observational experiment would be to treat the time since fire as a fixed effect, and the sample sites as a random effect and then apply a mixed effects model to analyze the difference. Using the 20 sample sites as a random effect is appropriate. The ecologist cannot enumerate plant diversity across the total area of each large landscape; the 20 sample sites per forest are a random sample of the possible levels of diversity in each stand of a given time-since-fire. Then, the F-ratio (which is the ratio of the between-stand to within-group stand) can be estimated correctly accounting for the contribution that the random effects have on the error term (Table 4.1). Studies that apply an incorrect denominator in the F-ratio may be inflating the risk of a Type I error through pseudoreplication. In Table  4.2, the F-ratio is the Mean square (Treatment), or MS(T), divided by Mean Square (Error), or MS(E). Thus, the numerator in the F-ratio (the MS (T)) contains the variation due to both the treatment (time since fire) and the variation due to the sample site locations. In this case, we cannot reliably infer that time since fire affects plant diversity—any observed variation in plant diversity could be due to the differences in the locations sampled since the sampling sites are nested within the treatment (the three stands of different time-since fire). This would match Hurlbert’s (1984) characterization of pseudoreplication as a test with an inappropriate error term. Note that in Table 4.1, one can not test for the effect of the treatment (the fixed effect) using an F-ratio of the MS(T) over the MS(E) as you would in Table 4.2, where site was ignored, and we only had the fixed effect of time since fire. To isolate the variation due to the treatment (time since fire) from variation due to the sites, one needs an F-ratio of MS(T) over MS(S(T)). By using MS(S(T)) in the denominator of the F-ratio, one isolates the treatment error correctly, and the issue of a pseudoreplication—in the sense of ambiguous F-ratios—vanishes! In many ecological studies, we sample across years. Imagine the ecologist re-­ surveying the sites in Fig. 4.1a in a second year. Sampling through time is common in long-term monitoring and environmental impact studies, but if done carefully, can be analysed in such a way that it is immune to accusations of pseudoreplication (Stewart-Oaten et al., 1986). If the data analysis in the first year showed that there

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4  Replication vs. Pseudoreplication: Are We Making Too Big a Deal of This?

a Stand A Time since fire = 10 years

Stand B Time since fire = 50 years

Sample site (20 per stand)

Stand C Time since fire = 100 years

10 m

10 km

b Stand A Time since fire = 10 years

Stand C Time since fire = 100 years

Stand B Time since fire = 50 years

Sample site (20 per stand)

Environmental gradient

10 m

10 km

Fig. 4.1 (a) Hypothetical landscape ecology study design, with three forest stands that are otherwise similar, but differ in their time since fire. Twenty sample sites (black dots) are randomly placed within each stand. At each site, the researcher employs a point-quarter technique with four 1 m × 1 m plots (inset circle) to sample ground vegetation. (b) The same hypothetical landscape as in Fig. 4.1a, but with the addition of an environmental gradient (this could be elevation, moisture, distance from a anthropogenic impact). The researcher allocates the 20 sample sites along two parallel transects within each stand

was higher variance at the site level than between the stands, we could justify treating the sites as fixed effects, and the two samples over time as random effects. This would remove sites from the denominator of the F-ratio. In this case, the allocation of variance could look like it does in Table  4.3. Note the change in the how we

4.2  What Is Pseudoreplication?

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Table 4.1  Expected mean squares for two factor ANOVA with fixed factor treatment, T, which has a levels, b levels of site S nested within treatments (as a random effect) and n replicates of S per T Sum of squares SST

Source of variability Treatment (T) (Fixed effect)

d.f. a–1

Site nested within Treatment S(T) (Random effect)

a(b–1) SSS(T)

Error (E)

ab(n– 1)

Expected mean square (EMS)

Mean square SST a −1

 2  n B2   2  n  B2 

SSST 

a  b  1 SSE

bn s 2  i a  1 i1

σ2 SSE N  a  1  n  1

In the example here (Fig. 4.1a), a = 3 (3 stands each with time since fire of 10, 50 and 100 years), b = 20 sites per stand and n = 4 quadrat sampling plots per site Table 4.2  Expected mean squares for tests for single-factor ANOVA with fixed factor treatment, T, which has a = 3 (3 stands each with time since fire of 10, 50 and 100 years), levels, and n = 80 (sample plot) replicates Source of variability Treatment (T)

Degrees of freedom a - 1

Sum of squares SST

Mean square

Expected mean square (EMS)

SST a −1

2 

Error (E)

(n – 1)

SSE

SSE  n  1

n s 2  i a  1 i1

σ2

Table 4.3  Expected mean squares for two factor ANOVA with fixed factor treatment, T (time since fire) and S (site) Source of variability Treatment (T) (Fixed effect)

d.f. a – 1

Sum of squares SST

Location nested within Treatment a(b – 1) SSS(T) S(T) (Fixed effect) Year (Y) (Random effect)

b – 1

SSY(S)

Error (E)

(a-1) (b-1)

SSE

Mean square SST a −1 SSST 

a  b  1 SSY  S 

Expected mean square (EMS)

2 

bn s 2  i a  1 i1

2 n

a b 1  ji2  a  b  1 i1 j 1

 2  t 2

b 1 σ2 SSE  a  1  b  1

T has a levels, and S has b levels of sites nested within treatments. The sites are sampled across t = 2 years (year (Y) as a random effect). There are n replicates of S per T. In the example here (Fig. 4.1a), a = 3 (3 stands each with time since fire of 10, 50 and 100 years), b = 20 sites per stand and n = 4 quadrat sampling plots per site

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4  Replication vs. Pseudoreplication: Are We Making Too Big a Deal of This?

calculate the denominator for the F-ratio here, compared to Table  4.1. We loose many degrees of freedom from the denominator when we treat sites as a fixed effect, but if we know that most of the variance is at the site level, then it makes sense to remove the variance due to site from the denominator. To offset the cost of lost degrees of freedom in the denominator, one could sample only half the sites in the second year. Note however, that normally when doing monitoring or environmental impact studies, one would not design the experiment this way, but rather would use a BACI analysis (Stewart-Oaten et al., 1986; Christie et al., 2020). This example illustrates the value of careful design, as the experimental design outlined here is not ideal for an impact study.

4.2.2  S  patial Autocorrelation Does Not Automatically Cause Pseudoreplication In landscape ecology, we are often quite conscious of the fact that the specific location in space matters and can influence our data. Let us imagine that the forests our ecologist is studying are oriented along a gradient (e.g., elevation); the researcher hypothesizes that the location of each sampling site along this gradient might also drive the understory diversity. In this case, the ecologist likely does not want to treat site as a random effect, but rather as a fixed effect. Thus, they may place the 20 sample plots quite deliberately, to try to capture the variation due to the elevation gradient (Fig. 4.1b). Such an experimental design might raise concerns about spatial autocorrelation. As explained above, part of the confusion around pseudoreplication is that there are different kinds of infractions rolled into the label ‘pseudoreplication’. Since one has to do with “ the actual physical space over which samples are taken” (Hurlbert, 1984, p. 190); this confusion about whether and when spatial autocorrelation contributes to pseudoreplication could lead to a rejected paper (Davies & Gray, 2015). To avoid problems, we need to partition the variance carefully. The EMS for this situation is shown in Table 4.4; notice how it differs from Table 4.1, and how the F-ratio to isolate for treatment effect can be obtained by the ratio of MS(T) over MS(E). The key here, is that any inference about the effect of the treatment (time since fire in this example) is limited to those locations, and cannot be extrapolated to other similar forest stands of the same time since fire, since there may be other, unmeasured variables influencing the data. In addition to the hypothetical experimental designs discussed above (Fig. 4.1), there may be complexities of interactions to deal with as well. The researcher might use a randomized block design to take samples within different habitat types (e.g., wetland vs. upland) within each stand. Hypotheses with a temporal dimension should explore using repeated-measures ANOVA. Such variations in the experimental design will allocate the error differently. Thus, taking the time to write out the EMS is useful. This takes careful thinking; I have included resources in the back of the book to help you. The text by Quinn and Keough (2002) is highly recommended.

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Table 4.4  Expected mean squares for two factor ANOVA with fixed factor treatment T, which has a levels Source of variability d.f. Treatment (T) (Fixed effect) a - 1

Location nested within Treatment S(T) (Fixed effect)

a(b – 1)

Error (E)

ab(n – 1)

Sum of squares SST

Mean square

SSS(T)

SSST 

SSE

SST a −1

Expected mean square (EMS)

2 

bn s 2  i a  1 i1 a

n 1

 n

SSE N  a  1  n  1

σ

2

b

   i 1 j 1

2 j i

a  b  1

2

In addition there are b levels of site, S, nested within treatments (as a fixed effect) and n replicates of S per T. In the example here (Fig. 4.1b), a = 3 (3 stands each with time since fire of 10, 50 and 100 years), b = 2 transects per stand, and n = 10 sites per transect

Careful experimental design is also important. An impact study will benefit from a different design than one with a hypothesis about ecological mechanisms. The list of suggested approaches in Table 1 of Davies and Gray (2015) and the classic paper on the design of field experiments by Eberhardt and Thomas (1991) are also highly recommended resources.

4.3  Responses and Debates There have been many papers written in response to Hurlbert (1984). These have put the issue of pseudoreplication in context for specific disciplines, including entomology (Chaves, 2010; Spurgeon, 2019), fire ecology (van Mantgem et al., 2001), cladistics (Brower, 2011; Hovenkamp, 2011), and fisheries research (Millar & Anderson, 2004; Nikinmaa et al., 2012; Bastos et al., 2013); as well as presented broader critiques and discussions (e.g., Oksanen, 2001, 2004; Cottenie & De Meester, 2003). They have also sometimes served to confuse the issue, so I will try to summarize the key takeaways from the debate for landscape ecologists here. A lively back-and-forth in the Journal of Comparative Psychology described pseudoreplication as a “pseudoproblem” (Schank & Koehnle, 2009), as “(still) a problem” (Freeberg & Lucas, 2009) and as an “ancient black art” (Koehnle & Schank, 2009). Some of the nuances of the debate in these articles are more germane to behavioural and psychology experiments than to landscape ecology, though the piece by Wiley (2009) which outlines the stark fact that all experimental designs have trade-offs will ring true in our discipline and was echoed by Koehnle and Schank (2009). Wiley (2009) discusses the challenges of large experiments in the sense of those with a large sample size (as can be done more easily in psychology), and so these may not seem relevant to landscape studies with limited replicates.

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However, the issue raised by Wiley (2009) of there being a higher risk of finding a statistically significant but biologically irrelevant small result with a larger sample size could hold true when sampling across a large spatial area. For example, if a large study area crosses some kind of sharp ecological or biophysical gradient we might expect to find significant differences in a response variable at the extreme ends of the study area that might be biologically irrelevant if the process we are interested in is actually happening at a smaller extent. Hurlbert’s response to the critiques published in this journal was a lengthy piece in which he directly took on Schank and Koehnle (Hurlbert, 2009). While some of the definitions in this piece are useful to today’s readers, Hurlbert’s attempts at humour have not aged as well. In a similar back-and-forth exchange in Oikos, Oksanen (2001) questions whether pseudoreplication is a “pseudoissue” (i.e., not really a concern). Oksanen’s view is particularly germane to landscape ecology experiments. He claims that “experimental ecologists fall primarily into two groups: those who do not see any problems with reducing spatial and temporal scales in order to obtain replication, and those who understand that experiments must be conducted in spatial and temporal scales relevant for the predictions to be tested” (Oksanen, 2001, p. 28). Since scale is of primary importance to landscape ecologists (see Chap. 5 for more about scale as it applies to experiments), this point by Oksanen (2001) merits consideration. Oksanen (2001) contends that many real-world problems require large(spatial) scale research (examples of which are discussed further in Chaps. 6 and 7), and offers four possible solutions for doing experiments in such systems. These are: (1) the use of microcosms (discussed in this book in Chap. 9); (2) limiting ourselves to predictions that are testable within limited spatial extents (see Chap. 5); (3) replication of controls but not treatments (discussed below) and; (4) carrying out experiments without replication (also discussed below). Hurlbert’s rejoinder in his 2004 paper was that Oksanen’s suggestion of replicated large-scale experiments, instead of replication within experiments was unrealistic. He makes the accusation that Oksanen may be lax in his use of the term “experiment”. In Hurlbert’s view, the term “experiment” should only be applied to a manipulated experiment with careful controls and that an observational study, while empirical, should not be considered “experimental”. He does concede that many disciplines (ecology amongst them) rely mainly on observational studies, and concedes that perhaps the adjectives “manipulative” and “mensurative” could be added to distinguish the two types of experiments (Hurlbert, 2004). As outlined in Chap. 2, the idea that observational studies can be considered experimental is consistent with the approach taken in this book, although I acknowledge that not all my colleagues will agree with me on this position. Indeed, Hurlbert (2004) outlines archetypical experiments at the level of whole lakes or islands that will be familiar to landscape ecologists. In his view, these are examples of large-scale experiments without treatment replication. Cottenie and De Meester (2003) agree that working at the appropriate scale is important and that in some cases, making the choice to work at a large extent means that experimental replicates may not be possible. They suggest that most of the critiques in Hurlbert’s original 1984 paper do not apply to such studies, but caution that ecologists should be well-versed with the critiques in the 1984 paper to avoid

4.3  Responses and Debates

45

problems. For example, Cottenie and De Meester (2003) express caution about using subsamples as replicates, when in fact they could represent pseudoreplicates (however, as discussed above, if F-ratios are configured properly, subsampling will not create the pseudoreplication issue of improper allocation of variance). The response to Hurlbert’s (1984) critique of ecological field experiments that is most germane to landscape ecologists is perhaps Hargrove and Pickering’s (1992) essay on the problem of pseudoreplication in large-extent studies. They took a bit of a “if you can’t beat ‘em, join ‘em” attitude, and suggested that, rather than eliminate pseudoreplication, ecologists working at large extents should embrace it. They referred to pseudoreplication as the sine qua non (Latin translation: the thing that is absolutely necessary) for regional ecology, meaning that without allowing (i.e., accepting that it is there) for pseudoreplication in studies, hypothesis testing within large-scale ecology research is not possible. Hargrove and Pickering (1992) proposed that ecologists focus on natural experiments, and coordinate these across space, time and scales as a substitute for classical experimental replicates. They suggest that classical experimentation, with rigorous controls and fully randomized and replicated sampling, is simply impossible and that landscape ecologists should stop beating themselves up trying to achieve it. Put bluntly, they advise that “regional ecology must infer what is true rather than falsify what is not” (Hargrove & Pickering, 1992, p. 255). Rather than slavish adherence to the hypothetico-­deductive approach (as described in Chap. 2) when working at landscape extents, they suggest that what they call “quasi-experiments” (equivalent to “natural experiments” as discussed in earlier chapters of this book) repeated across different places can, over time, yield inferences, even if they can not directly infer cause-effect relationships. They advise that competing hypotheses could be tested using more classical approaches at smaller extents and then used to infer processes based on patterns observed at larger scales. They offer two other concrete suggestions; space-for-time substitutions, a technique developed by some of the earliest ecologists (and described in Chap. 2) and a (then) newer technique (which they describe as “controversial” in 1992) of meta-analysis. I do not think we need to be as defeatist as Hargrove and Pickering (1992) and give up trying to do experiments; indeed, as this book tries to show, I think rigorous experiments are very possible for landscape ecology. Landscape ecologists should be aware of the risks of a reviewer accusing them of pseudoreplication. Pseudoreplication is an ambiguous term. Most accusations centre on a misunderstanding of how the researcher partitioned the variance, or whether aspects of the design, like allocation of sample sites in space, are fixed or random. Thus, landscape ecologists need to be prepared to defend charges of improper design, and specify the correct model (see Table 4.1 above in contrast to Table 4.2). The examples above present only a simple ANOVA, other approaches such as nested or repeated-measures ANOVA may be more appropriate for a particular hypothesis test and assist with correct partitioning of error. Statistical tools, such mixed-effects models, or multi-level modelling, can be specified to address some of perceived issues of pseudoreplication (Koehnle & Schank, 2009). Presenting effect sizes instead of p-values (Oksanen, 2001) is another useful strategy. In any case, a

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4  Replication vs. Pseudoreplication: Are We Making Too Big a Deal of This?

dogmatic approach to the issue of pseudoreplication is not useful (Davies & Gray, 2015). Davies and Gray (2015) suggest that researchers (and reviewers!) ask three key questions when confronted with a study design where there may be accusations of pseudoreplication. These include addressing whether pseudoreplication has been accounted for in the hypothesis formulation (including delineation of sources of error, see section on EMS tables above) and in the inferences drawn from the study (recommendations about inference and inductive logic were also proposed by Oksanen (2001) and by Cottenie and De Meester (2003)). Unfortunately, thinking philosophically about hypotheses and the scientific method is often under-­ emphasized in scientific training. Researchers who have taken time to familiarize themselves with some of the key readings on the philosophy of science will be better equipped to carry out a scientific study that will not be open to accusations of pseudoreplication, and more empowered to rebut reviewer critiques when faced with such charges. The summary in Chap. 2, and suggested readings in the Resources section of this book, offer some key books and papers to consider in this vein. A further thought experiment is to consider whether a fully replicated or manipulated study is possible (Davies & Gray, 2015). As pointed out above (Hargrove & Pickering, 1992; Oksanen, 2001; Cottenie & De Meester, 2003), some questions apply at large spatial extents, and replication or manipulation is simply not feasible. In that case, a “natural experiment” will suffice, even if the layout could be accused of having a less-than-ideal design if it were translated into petri dishes on a lab bench. Finally, careful use of appropriate statistical analysis (with properly articulated EMS) will insulate against problematic inferences (Davies & Gray, 2015). This book is not a statistics text so will not go into detail on these approaches—but I hope it will convince you that landscape ecologists need solid statistical skills!

4.4  P  otential Solutions to Address Charges of Pseudoreplication While there has been some acknowledgement that Hurlbert’s (1984) critiques apply more to highly manipulative experiments using classical statistics, many ecologists still find they are accused of pseudoreplication, and Davies and Gray (2015) showed that this can slow down research and result in potentially unwarranted rejections of papers by journals. Herewith then, some suggestions for experimental design that can help landscape ecologists avoid charges of pseudoreplication. They are not a guarantee that a reviewer will not accuse you of pseudoreplication, so in addition to carefully designing your experiment, you would be wise to read the literature yourself and ensure your sampling design and statistical analyses are airtight!

4.4  Potential Solutions to Address Charges of Pseudoreplication

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4.4.1  Space-for-Time Substitutions In their critique of the way large-scale ecologists have distanced themselves from natural history, Guidetti et al. (2014, p. 5), labelled space-for-time substitutions as “not properly experimental”. Confusion over how the research has allocated variation due to space and/or time in the EMS can lead to accusations of pseudoreplication, as we saw above. Nonetheless, ecologists working at larger spatial extents have often made use of space-for-time substitutions as a means to test hypothesis (e.g., Lengyel et  al., 2012; Knuckey et  al., 2016; LeClerc & Wiersma, 2017). As discussed in the previous two chapters, the early field ecology by William Cooper, in Glacier Bay, Alaska, used sample locations at different distances from the glacial front as snapshots of different temporal stages of succession. However, others have suggested that the utility of space-for-time substitutions is limited (Mimet et  al., 2016). This could be due to spurious or masked thresholds (Maron et al., 2012) created when the two spaces compared have different site characteristics or disturbance history (Derderian et al., 2016). Others have suggested that differences in configuration of patches may be key drivers of changes in biodiversity and do not vary the same ways in space as in time (Bonthoux et  al., 2013; Mimet et  al., 2016). Researchers who want to use two or more different spaces as snapshots in time would be wise to carry out a careful natural history study of each site to try to understand their dynamics as much as possible. A further recommendation would be to collaborate with environmental historians, who can lend their expertise with documentary evidence to help assess how and why the historical use and/or management of the sites might affect their trajectories. Often the processes that led to contemporary patterns are different from those assumed by natural scientists (see Langston (1995) and Donahue (2007) for examples of environmental histories of the Pacific Northwest and New England respectively, that throw new light on ecological assumptions about landscape trajectories through time). Environmental historians can help collate evidence for historical activities and patterns, and interdisciplinary collaborations between scientists and historians (e.g., Steen-Adams et al., 2015) can yield valuable insights on past land use patterns and help researchers decide whether two or more landscapes could be used appropriately as spatial substitutes for temporal samples.

4.4.2  Meta-analysis The technique of meta-analysis has gained more widespread acceptance since proposed by Hargrove and Pickering (1992) as a solution to pseudoreplication in landscape ecology and further endorsed as a solution by Oksanen (2001). A meta-analysis is a type of statistical analysis that looks at data from multiple independent studies that address the same research question with the goal to infer beyond the limits of any one study. Meta-analyses offer a rigorous, transparent approach with strong

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4  Replication vs. Pseudoreplication: Are We Making Too Big a Deal of This?

inferential power, if done properly. Koricheva et al. (2013) is an excellent text for those embarking on a meta-analysis. Landscape ecologists have harnessed meta-­ analyses to assess impacts of land degradation due to mining activities on small mammals (Lawer et al., 2019); to investigate how landscape patterns influence ecosystem services (Duarte et al., 2018), to test the intermediate disturbance hypothesis (Yeboah & Chen, 2016) and to synthesize across manipulative experiments on carbon-­cycling (Song et al., 2019). Meta-analyses of landscape studies which themselves may have little to no replication can be challenging, given that lack of replicating means limited variances and challenges to determine effect sizes accurately without bias-correction (see Doncaster and Spake (2018) for suggested techniques for meta-analysis in this case). Meta-analysis is not considered experimentation (Hargrove & Pickering, 1992) and so will not be discussed in detail in this book. However, in addition to the text referenced above, I have included some resources in the back of the book (see under the “Chap. 4” heading) for those interested in learning more about doing a meta-analysis.

4.4.3  S  imple Pseudoreplication – Or “Don’t Replicate/ Don’t Worry” In his widely-cited paper, Hurlbert (1984) points out that the most common type of field experiment in ecology is one with one treatment and one control. He acknowledges the challenge of replication with large-extent systems and admits that “(t)his is neither surprising nor bad” (Hurlbert, 1984, p. 199). In his reply to Oksanen, he provides further examples of large-scale studies in which replication of treatment is difficult and suggests that such experiments (e.g., the Hubbard Brook experiment, or work in the Experimental Lakes of Ontario) “have led to significant new insights, corroborated particular theories and advanced science” (Hurlbert, 2004, p. 595). If effects are large, or anticipated to be so, then an n of 1 treatment and 1 control may be the best means of gaining inference about that system, so long as the researcher does not try to apply statistical tests to this experiment or make inferences beyond the limits of the study system.

4.4.4  Experimental Design The crux of Hurlbert’s first paper on the topic of pseudoreplication was that design of field experiments should match analytical methods (Hurlbert, 1984). Koehnle and Schank (2009) disagreed. They felt that analytical methods should match experiments. So which comes first? Experimental design or analytical methods? Maybe they happen concurrently. I encourage my students to develop their research hypotheses based on a combination of deductive reasoning based on theory in their

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sub-field and inductive reasoning based on preliminary observations of their study system. From there, we make predictions—predictions that are statistical hypotheses constructed as if/then statements. For example, “if research hypothesis is supported, then…” where the then is an outline of what we expect to see at the end of the study if our system works the way we hypothesize that it does. I encourage them to sketch out “toy graphs” of what they feel this evidence will look like; that is, what does the then look like that will fail to falsify the if. If we fail to falsify the hypothesis, and our statistical tests are robust, then we will be able to make strong inferences about our research hypothesis. The toy graphs help us to address the issue of statistical robustness. Unfortunately, recent research by Betts et al. (2021) shows that good hypothesis formulation is often absent in ecological research. By looking at the type of data we anticipate needing to test our hypothesis, we can start to think about the type of statistical tools we may apply and then anticipate issues of sampling and/or experimental design that we need to consider in order to meet the assumptions of those statistical tests. Thinking about the sources of error and writing out the EMS before starting out is a valuable and highly recommended exercise as well. Thus, in my research group, we try to consider experimental design and analytical methods simultaneously, and do so while developing our hypotheses. Careful consideration of sources of bias in experimental design at the outset will also avoid future problems during analysis (Christie et al., 2020). Although dated, Eberhardt and Thomas’ (1991) typology of field experimental designs is a useful reference at this stage, and the questions posed by Davies and Gray (2015) can help with the design of natural experiments. Key to successful experimental design is careful consideration of how error is portioned between the independent variables. Christie et al. (2020) offer that estimation error is a result of the combined effects of design bias, modelling bias, and statistical noise. We can try to reduce statistical noise with increased sample size, but as pointed out above, this is difficult to do in some landscape studies. We can reduce modelling bias by considering model structure (e.g., linear/non-linear, mixed effects) and possible interactions a priori (Wilk & Kempthorne, 1955). This will help the researcher to correctly identify the proper F-ratio and design a study that will be robust to spurious accusations of pseudoreplication. Consideration of the biases intrinsic in our choice of study design is also necessary. Christie et  al. (2020) compare six common experimental designs and show that controlled and/or randomized designed (e.g., a BACI over a B-A study) reduced bias in estimates (see also Stewart-Oaten et al., 1986). There are excellent texts (e.g., Krebs, 1989; Quinn & Keough, 2002) that outline different options for experimental design that may suggest possibilities that you may have not yet considered.

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4.4.5  Sampling Because landscape ecologists will often be carrying out observational experiments with one treatment and one control, and (sub)sampling within each, some careful consideration of sampling design is warranted. The statistical tools available to the average ecologist today are much more sophisticated than when Hurlbert (1984) wrote his treatise (Yoccoz et al., 2001; Mörsdorf et al., 2015; Williams & Brown, 2019), so a meticulous ecologist should be able to design a robust sampling scheme that is appropriate for the hypothesis being tested. The assumption that samples have known mean-variance that is representative of the population is no longer necessary. Probabilistic sampling, in which the probability of selecting a sampling unit can be reliably estimated, allows for collection of data that can be analysed statistically, but limits the inference to the sample. Inferences about the wider population will be limited. Knowledge about the system you are sampling—for example whether it follows gradients or has thresholds can help with appropriate sampling designs (Albert et al., 2010). Diverse modelling methods beget different sampling designs (Williams & Brown, 2019), further stressing the value of considering your analytical techniques early in the research process. When sampling plots within landscapes, we need to make careful consideration about what is the sampling unit. Mörsdorf et al. (2015) described spatial sampling units that could be defined formally (for example using a GIS), or subjectively in the field based on biotic and/or abiotic attributes. These decisions influence the interpretations from the study, so clarity on the ways in which you define your sampling units is of utmost importance. For an excellent case study showing how sampling design and statistical analysis can affect interpretation in a large scale study (with one replicate), see Peterson et  al.’s (2001) comparison of four studies of the impacts of the Exxon-­ Valdez oil spill. There is no “right” or “wrong” way to sample within a landscape. How you design your sampling is driven by the nature of the scientific question. From there, the sampling depends on the spatial and biophysical structure of the landscape, the response variable(s) you are interested in, the modelling or statistical tools at your disposal, your available resources, and the type of inference you hope to draw. Careful thought about distinguished fixed vs. random effects is also necessary. As long as you carefully think about why you are sampling first, and then design how you will sample, you should be able to defend yourself in the face of ‘knee-jerk’ accusations of pseudoreplication (Davies & Gray, 2015).

4.5  The Bottom Line In their discussion of whether and how pseudoreplication might affect landscape ecology, Hargrove and Pickering (1992, p. 252) wrote “For fear of pseudoreplicating, landscape ecology is becoming more reductionist when the object is to become more holistic. The sanctioned conceptual framework and experimental techniques

References

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available to regional ecologists are inconsistent with the nature of regional ecology. This deep conflict has resulted in stagnation.” I would hope that our field has not suffered from stagnation for the last three decades! Yet, pseudoreplication is still frequently misunderstood and mischaracterized (Colegrave & Ruxton, 2018). There are recent examples where the progress of research has been slowed down by either spurious accusations of pseudoreplication, or misunderstanding on the part of researchers and/or reviewers on how to deal with samples that do not fit the assumptions of “classical” experimental design or statistical tests (Davies & Gray, 2015). The real-world problems that landscape ecologists frequently tackle often require large-scale experiments (Schindler, 1998; Barley & Meeuwig, 2017) wherein it might appear at first glance that we are pseudoreplicating. Trade-offs between realism and replication are necessary and we should not apologize for them. At the same time we can advance our field (and hopefully avoid stagnation!) by considering complementary methods (e.g., micro- or mesocosm studies, in silico experiments, model systems) to large-scale observational studies that can increase our ability to extrapolate through space and time and help us to elucidate the mechanisms that drive the landscapes we are fascinated with. I hope that some of the ideas in this book can help achieve those goals.

References Adedoja, O., Kehinde, T., & Samways, M. J. (2019). Time since fire strongly and variously influences anthophilous insects in a fire-prone landscape. Ecosphere, 10, e02849. https://doi. org/10.1002/ecs2.2849 Albert, C.  H., Yoccoz, N.  G., Edwards, T.  C., et  al. (2010). Sampling in ecology and evolution – Bridging the gap between theory and practice. Ecography, 33, 1028–1037. https://doi. org/10.1111/j.1600-­0587.2010.06421.x Barley, S. C., & Meeuwig, J. J. (2017). The power and the pitfalls of large-scale, unreplicated natural experiments. Ecosystems, 20, 331–339. https://doi.org/10.1007/s10021-­016-­0028-­5 Bastos, A.  C., Monaghan, K.  A., Pestana, J.  L. T., et  al. (2013). A comment on the editorial “Replication in aquatic biology: The result is often pseudoreplication”. Aquatic Toxicology, 126, 467–470. https://doi.org/10.1016/j.aquatox.2012.11.003 Bataineh, A. L., Oswald, B. P., Bataineh, M., et al. (2006). Spatial autocorrelation and pseudoreplication in fire ecology. Fire Ecology, 2, 107–118. https://doi.org/10.4996/fireecology.0202107 Betts, M. G., Hadley, A. S., Frey, D. W., et al. (2021). When are hypotheses useful in ecology and evolution? Ecology and Evolution, 1–15. https://doi.org/10.1002/ece3.7365 Bonthoux, S., Barnagaud, J., Goulard, M., & Balent, G. (2013). Contrasting spatial and temporal responses of bird communities to landscape changes. Oecologia, 172, 563–574. https://doi. org/10.1007/s00442-­012-­2498-­2 Boucher, D., De Grandpré, L., Kneeshaw, D., et  al. (2015). Effects of 80 years of forest management on landscape structure and pattern in the eastern Canadian boreal forest. Landscape Ecology, 30, 1913–1929. https://doi.org/10.1007/s10980-­015-­0220-­6 Boucher, Y., Perrault-Hébert, M., Fournier, R., et  al. (2017). Cumulative patterns of logging and fire (1940–2009): Consequences on the structure of the eastern Canadian boreal forest. Landscape Ecology, 32, 361–375. https://doi.org/10.1007/s10980-­016-­0448-­9 Brower, A.  V. Z. (2011). Stability, replication, pseudoreplication and support. Cladistics, 26, 112–113.

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Chaves, L.  F. (2010). An entomologist guide to demystify pseudoreplication: Data analysis of field studies with design constraints. Journal of Medical Entomology, 47, 291–298. https://doi. org/10.1603/me09250 Christie, A. P., Abecasis, D., Adjeroud, M., et al. (2020). Quantifying and addressing the prevalence and bias of study designs in the environmental and social sciences. Nature Communications, 11, 6377. https://doi.org/10.1038/s41467-­020-­20142-­y Colegrave, N., & Ruxton, G. D. (2018). Using biological insight and pragmatism when thinking about pseudoreplication. Trends in Ecology & Evolution, 33, 28–35. https://doi.org/10.1016/j. tree.2017.10.007 Cottenie, K., & De Meester, L. (2003). Comment to Oksanen (2001): Reconciling Oksanen (2001) and Hurlbert (1984). Oikos, 100, 394–396. Davies, G. M., & Gray, A. (2015). Don’t let spurious accusations of pseudoreplication limit our ability to learn from natural experiments (and other messy kinds of ecological monitoring). Ecology and Evolution, 5, 5295–5304. https://doi.org/10.1002/ece3.1782 Derderian, D. P., Dang, H., Aplet, G. H., & Binkley, D. (2016). Bark beetle effects on a seven-­ century chronosequence of Engelmann spruce and subalpine fir in Colorado, USA. Forest Ecology and Management, 361, 154–162. https://doi.org/10.1016/j.foreco.2015.11.024 Donahue, B. (2007). The great meadow: Farmers and the land in colonial Concord. Yale University Press. Doncaster, C. P., & Spake, R. (2018). Correction for bias in meta-analysis of little-replicated studies. Methods in Ecology and Evolution, 9, 634–644. https://doi.org/10.1111/2041-­210X.12927 Duarte, G. T., Santos, P. M., Cornelissen, T. G., et al. (2018). The effects of landscape patterns on ecosystem services: Meta-analyses of landscape services. Landscape Ecology, 33, 1247–1257. https://doi.org/10.1007/s10980-­018-­0673-­5 Eberhardt, L.  L., & Thomas, J.  M. (1991). Designing environmental field studies. Ecological Monographs, 61, 53–73. https://doi.org/10.2307/1942999 Eisenhart, C. (1947). The assumptions underlying analysis of variance. Biometrics, 3, 1–21. Flaherty, C. (2002). Canceling emeritus. Inside Higher Ed. Fletcher, R. J., & Hutto, R. L. (2008). Partitioning the multi-scale effects of human activity on the occurrence of riparian forest birds. Landscape Ecology, 23, 727–739. https://doi.org/10.1007/ s10980-­008-­9233-­8 Freeberg, T.  M., & Lucas, J.  R. (2009). Pseudoreplication is (still) a problem. Journal of Comparative Psychology, 123, 450–451. https://doi.org/10.1037/a0017031 Guidetti, P., Parravicini, V., Morri, C., & Bianchi, C. N. (2014). Against nature? Why ecologists should not diverge from natural history. Vie Milieu, 64, 1–8. Hargrove, W. W., & Pickering, J. (1992). Pseudoreplication: A sine qua non for regional ecology. Landscape Ecology, 6, 251–258. https://doi.org/10.1007/BF00129703 Hovenkamp, P. (2011). Stability, replication, pseudoreplication, support and consensus — A reply to Brower. Cladistics, 27, 4–5. Hurlbert, S. H. (1984). Pseudoreplication and the design of ecological field experiments. Ecological Monographs, 54, 187–211. https://doi.org/10.2307/1942661 Hurlbert, S. H. (2004). On misinterpretations of pseudoreplication and related matters: A reply to Oksanen. Oikos, 104, 591–597. https://doi.org/10.1111/j.0030-­1299.2004.12752.x Hurlbert, S.  H. (2009). The ancient black art and transdisciplinary extent of pseudoreplication. Journal of Comparative Psychology, 123, 434–443. https://doi.org/10.1037/a0016221 Ims, R. A. (2005). The role of experiments in landscape ecology. In J. A. Wiens & M. R. Moss (Eds.), Issues and perspectives in landscape ecology (pp. 70–78). Cambridge University Press. Kloor, K. (2018). When bigotry is cloaked. Discovery Magazine Online Newsletter. Knuckey, C. G., Van Etten, E. J. B., & Doherty, T. S. (2016). Effects of long-term fire exclusion and frequent fire on plant community composition: A case study from semi-arid shrublands. Austral Ecology, 41, 964–975. https://doi.org/10.1111/aec.12388 Koehnle, T. J., & Schank, J. C. (2009). An ancient black art. Journal of Comparative Psychology, 123, 452–458. https://doi.org/10.1037/a0017435

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Schank, J. (2001). Is pseudoreplication a pseudo-problem? American Zoologist, 41, 1577. Schank, J.  C., & Koehnle, T.  J. (2009). Pseudoreplication is a pseudoproblem. Journal of Comparative Psychology, 123, 421–433. https://doi.org/10.1037/a0013579 Schindler, D. W. (1998). Replication versus realism: The need for ecosystem-scale experiments. Ecosystems, 1, 323–334. https://doi.org/10.1007/s100219900026 Schulte, L. A., Mladenoff, D. J., Crow, T. R., et al. (2007). Homogenization of northern U.S. Great Lakes forests due to land use. Landscape Ecology, 22, 1089–1103. https://doi.org/10.1007/ s10980-­007-­9095-­5 Song, J., Wan, S., Piao, S., et al. (2019). A meta-analysis of 1,119 manipulative experiments on terrestrial cabon-cycling repsonses to global change. Nature Ecology & Evolution, 3, 1309–1320. Spurgeon, D. W. (2019). Common statistical mistakes in entomology: Pseudoreplication. American Entomologist, 65, 16–18. https://doi.org/10.1093/ae/tmz003 Steen-Adams, M.  M., Langston, N., Adams, M.  D. O., & Mladenoff, D.  J. (2015). Historical framework to explain long-term coupled human and natural system feedbacks: Application to a multiple-ownership forest landscape in the Northern Great Lakes region, USA. Ecology and Society, 20, 28. https://doi.org/10.5751/ES-­06930-­200128 Stewart-Oaten, A., Murdoch, W. W., & Parker, K. R. (1986). Environmental impact assessment : “Pseudoreplication” in time? Ecology, 67, 929–940. Stroup, W. W. (2013). Generalized linear mixed models. CRC Press. Taillie, P. J., Burnett, R. D., Roberts, L. J., et al. (2018). Interacting and non-linear avian responses to mixed-severity wildfire and time since fire. Ecosphere, 9, e02291. https://doi.org/10.1002/ ecs2.2291 Turner, M. G. (2005). Landscape ecology in North America: Past, present, and future. Ecology, 86, 1967–1974. https://doi.org/10.1890/04-­0890 van Mantgem, P., Schwartz, M., & Keifer, M. (2001). Monitoring fire effects for managed burns and wildfires: Coming to terms with pseudoreplication. Natural Areas Journal, 21, 266–273. Wiens, J. A., & Milne, B. T. (1989). Scaling of “landscapes” in landscape ecology, or, landscape ecology from a beetle’s perspective. Landscape Ecology, 3, 87–96. https://doi.org/10.1007/ BF00131172 Wiley, R. H. (2009). Trade-offs in the design of experiments. Journal of Comparative Psychology, 123, 447–449. https://doi.org/10.1037/a0016094 Wilk, M. B., & Kempthorne, O. (1955). Fixed, mixed, and random models. Journal of the American Statistical Association, 50, 1144–1167. Williams, B. K., & Brown, E. D. (2019). Sampling and analysis frameworks for inference in ecology. Methods in Ecology and Evolution, 10, 1832–1842. Wu, J., & Hobbs, R. (2002). Key issues and research priorities in landscape ecology: An idiosyncratic synthesis. Landscape Ecology, 17, 355–365. https://doi.org/10.1023/A:1020561630963 Yeboah, D., & Chen, H.  Y. H. (2016). Diversity–disturbance relationship in forest landscapes. Landscape Ecology, 31, 981–987. https://doi.org/10.1007/s10980-­015-­0325-­y Yoccoz, N. G., Nichols, J. D., & Boulinier, T. (2001). Monitoring of biological diversity in space and time. Trends in Ecology & Evolution, 16, 446–453. Zlonis, E.  J., & Niemi, G.  J. (2014). Avian communities of managed and wilderness hemiboreal forests. Forest Ecology and Management, 328, 26–34. https://doi.org/10.1016/j. foreco.2014.05.017 Zong, S., He, H., Liu, K., et al. (2018). Typhoon diverged forest succession from natural trajectory in the treeline ecotone of the Changbai Mountains, Northeast China. Forest Ecology and Management, 407, 75–83. https://doi.org/10.1016/j.foreco.2017.09.051

Chapter 5

Scale—We All Talk About It; What Do We Do With It?

What is an ‘appropriate’ scale depends in part on the questions one asks. –John Wiens. (From Wiens JA (Wiens, 1989) Spatial scaling in ecology. Funct Ecol 3(4): 385–397)

5.1  Introduction Scale is one of the fundamental concepts in landscape ecology; indeed some would say landscape ecologists are “obsessed” with scale. Although scale is discussed in ecology broadly (e.g., Gardner et al., 2001; Schneider, 2001a, b), the definitions and concepts of scale within landscape ecology are specific (Forman & Godron, 1981) and borrow extensively from geography (Meentemeyer, 1989). Scale concepts are not unique to landscape ecology; they are highly germane in fields such as geography, remote sensing and modelling (Schneider, 2001a) and landscape ecologists have borrowed extensively from these fields of study to develop an understanding of scale concepts. Seminal readings on scale issues beyond those cited in this chapter are included under the Chap. 5 heading in the “Resources” section of this book. In this chapter, I will focus on how concepts of scale are important considerations for experimental work in landscape ecology and show how scale can affect how we measure or define a landscape; and how we interpret a biological response, in particular how we estimate a relationship between elements of landscape pattern and a biological response. Early work in the discipline helped develop definitions of scale (Wiens, 1989), including emphases of two key components of scale; grain and extent (e.g., Kotliar & Wiens, 1990); see Box 5.1 for definitions of key terms and concepts in this chapter. Grain and extent are probably two of the concepts landscape ecologists learn early on in their training as a way to describe a landscape under study. However, it is interesting to note how Wiens’ (1989) definitions of grain and extent focus on the observer’s perspective and Kotliar and Wiens’ (1990) focuses on the organisms’ perspective. When conducting experiments, researchers should not only be aware of © Springer Nature Switzerland AG 2022 Y. F. Wiersma, Experimental Landscape Ecology, Landscape Series 29, https://doi.org/10.1007/978-3-030-95189-4_5

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how grain and extent affect experimental outcome, but also be clear about which perspective they are adopting in defining their particular grain/extent. As well, they may need to consider that the scale at which the ecological processes and/or patterns of interest are operating may not match the scale at which they are managed (Mayer, 2019; Mayer et al., 2016). Others have explored how hierarchy theory can be applied to landscape ecology concepts in both space and time (e.g., O’Neill et  al., 1989; Urban et  al., 1987). Hierarchy theory, borrowed from systems theory research (Pattee, 1973), has formed a useful framework for understanding how ecological patterns and processes are nested in space and time. As well hierarchy theory as a concept has been leveraged to extrapolate information across scales (Schneider, 2001b; Urban, 2005; Wu, 1999). Hierarchy theory (Allen & Starr, 1982; Pattee, 1973) helps to explain and understand systems that “have a certain type of organized complexity” (Urban et al., 1987, p. 121). In the context of landscape ecology, hierarchy concepts help to define and explain how lower level components (e.g., individual trees) generate higher-­ level patterns (e.g., stand size, shape and composition) and processes (e.g., forest insect outbreaks, nutrient cycles), and, conversely, how higher-level patterns constrain lower-level patterns and processes. Generally, higher levels of organization (e.g., biomes) have processes that occur more slowly and across larger spatial extents than lower ones (e.g., forest stands) (Urban et al., 1987). Figure 5.1 illustrates a space-time hierarchy figure taken from Delcourt et al. (1982). Interestingly,

Fig. 5.1  Example of a space-time diagram showing the hierarchical nature of disturbance regimes, biotic responses and vegetation patterns. (Reproduced from Delcourt et al. (1982) with permission from Elsevier)

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these types of figures, which were fundamental to organizing the thinking of early (terrestrial) landscape ecologists are borrowed from the diagrams developed by oceanographer Henry Strommel in 1963 (Pittman et al., 2018; Vance & Doel, 2010). A critical examination of where a pattern or phenomenon occurs within a hierarchical structure can help to identify which are the critical ecological processes that affect it, which in turn can help inform experimental design. Kotliar and Wiens (1990) used a hierarchical model to address questions about foraging theory. Foraging theory bases its predictions on the assumption of within-patch homogeneity, when in reality, we know that there exists both within- and between-patch heterogeneity. In addition, patch boundaries are not fixed and depending on the scale of view and the research question, the size and boundaries of a patch can be delineated different ways. For example, we could consider an entire national park surrounded by a more altered matrix to be a “patch”. However, within that park, we could also define smaller patches, for example, based on different stand types in a forest, or delineated based on forested vs. non-forested land cover. Hierarchy theory is a useful lens that can help assess at which level in a hierarchy the “patch” is best delineated for a particular question. For example, for a browsing ungulate, the “patch” can be a tree seedling, a stand of trees, or the home range they inhabit. Mayor et al. (2009) discuss how ecologists can leverage this view in the development of habitat selection models at different scales. Hierarchy theory provides one theoretical framework for understanding scale. On a more practical level, scale issues can also become testable hypotheses—for example, whether home range size is dependent on the mass of the organism (as posited by Kotliar & Wiens, 1990). Related to hierarchy issues are cross-scale studies (e.g., Lan et al., 2015) and the sometimes-confounding phenomenon of contrasting results across different scales. For example, patch-level nitrogen-enrichment experiments show reductions in species richness, but at landscape extents, the negative effect of nitrogen enrichment is weaker (Lan et al., 2015). This is an example of the issues and challenges with scaling rules—discussed in more detail below. The patch-mosaic model is another framework for understanding scale, which emphasizes patch-patch interaction. Depending upon at what scale the researcher defines and analyses patches, different patterns may emerge (Castilla et al., 2009). For example, Turner and Romme (1994) examined fire dynamics, and identified that climate controls crown fire behaviour at broad scales, and topography and spatial distribution of fuel influence fire spread at smaller scales. Others have shown how organisms’ response to habitat differs across patch-landscape scales (e.g., Staveley et al., 2020). Researchers have further linked patch-mosaic concepts with metacommunity perspectives across scales in different systems, including fluvial ecosystems (Winemiller et  al., 2010) and experimental microcosms (Limberger & Wickham, 2012).

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5.2  Overlooked Dimensions of Scale Most of the discussion about scale in landscape ecology has focused on spatial components. Grain and extent play heavily into the use and application of remotely sensed data, however these concepts apply to other types of data as well, and are important to bear in mind in the context of empirical investigations. Time is a type of data where the grain and extent concepts are particularly germane. If taking temperature and humidity measurements with a data logger, one has a choice of grain (frequency of individual observations) and extent (the overall number of days/ weeks/months/years) for the data collection that is usually limited only by the storage capacity of the device. Which grain/extent one choses to sample at may depend on the perception of the organism(s) under study. Time plays a role in concepts of ecological hierarchy as well, with many of the spatial patterns scaling in conjunction with temporal patterns. For example, vegetation patterns in a forest follow hierarchical space-time dynamics that can be tightly correlated (Delcourt et al., 1982; Urban et al., 1987). Disturbances such as tree falls happen at shorter time intervals and smaller spatial extents when compared to once-in-a-century events like fires that disturb larger areas. In the ungulate example of different patch definitions above, if we are asking a question about foraging over the scale of minutes, then individual saplings are the appropriate patch. If we are looking at foraging decisions over an individual’s lifetime, then forest stands within the home range may be more appropriate. We can also think of taxonomic data as having scale dimensions. Grain (or taxonomic resolution to use the language of taxonomy) in particular is an important consideration that affects data quality. How many ground cover plot data sets have categories for “mosses and lichens”; a level of taxonomic resolution that in reality can represent dozens of species? This generalization of data can have important consequences for management decisions. For example, forest managers often use herbicides to remove competing species from the ones desired. Researchers have suggested that particular herbicides can have a negative effect on “lichens” and grouped these a single unit of assessment (e.g., Mallik et al., 2002; Mihajlovich & Blake, 2004). However, lichen diversity in boreal forests can be 10–30 species within a 10 × 10 m plot. In addition to the taxonomic diversity, even within a genus there is morphological and chemical diversity between species that might affect sensitivity to herbicides. Indeed McMullin et  al. (2012) demonstrated varying degrees of sensitivity to two types of herbicides, mostly correlated to morphology, with species with a highly branched structure being the more sensitive. This nuance is lost when taxonomic resolution is generalized to the life form (e.g., “lichens”). A related concept to scale is that of fractal dimension. Fractal dimensions quantitatively describe those features that are more complex than a 1-dimensional shape (i.e., a straight line) and not a fully 2-dimensional shape (e.g., a plane-filling shape like a square or circle). Fractals are common patterns in nature, for example, in tree branching or in snowflakes (Mandelbrot, 1983). The idea that landscape pattern could be described in terms of fractal dimension was an early development in the

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field of landscape ecology (see Cain et al., 1997; With, 1994). Fractals have been useful to create neutral models of landscapes in silico which can be compared to real landscapes (Gardner et al., 1987; With et al., 1999). Fractal dimensions are also useful for cross-scale comparisons (Schneider, 2001b) and Feng and Liu (2015) demonstrated how to use fractal dimension to quantify how pattern metrics change with grain.

5.3  Challenges with Scale and Experiments When doing experimental work in landscape ecology, it is important to consider the effects that scale may have on observations or on the phenomenon of interest. Many observational experiments in landscape ecology compare two (or more) landscapes in space and/or time to assess how a particular process affects landscape pattern or landscape change. For example, landscape ecology papers have compared landscape change through time following anthropogenic disturbance (e.g., an open pit mine) to a control area (e.g., a nearby national park; LeClerc & Wiersma, 2017) or compared forest landscape patterns following a natural disturbance such as fire (e.g., Kashian et  al., 2004) to a control area. Often the comparison is quantified using metrics, for example the suite available in FRAGSTATS (McGarigal & Marks, 1995). Costanza et al. (2019) summarized the long history of use of metrics in the discipline in a special issue of Landscape Ecology (vol 34(9)) devoted to the topic of pattern analysis. A detailed discussion of metrics is not the goal of this chapter; most landscape ecologists will be familiar with the application of metrics or empirical measurements of one sort or another to quantify complex spatial composition and configuration of their landscapes. While the breadth of metrics and the facility with which they can be generated makes doing empirical analysis of landscapes seem straightforward, researchers should be cautious when applying them. Many studies, using both real and simulated data, have shown that landscape metrics can be highly sensitive to scale effects, particularly the spatial grain and extent of the data (Cain et al., 1997; Feng & Liu, 2015; Li & Wu, 2004; Turner et al., 1989; Wu, 2004; Wu et al., 2002). Not all metrics respond to different scales in the same way; Feng and Liu (2015) demonstrated that metrics describing area, edge, shape and aggregation characteristics followed fractal scaling laws and thus could be compared across scales. However, Li et al. (2005) showed that most metrics were sensitive to scale effects. Because metrics are such a common tool in observational experiments, researchers should take the time to consider carefully which metric to use. Researchers debating what landscape pattern metrics to use should consult several of the comprehensive reviews (Cain et al., 1997; Feng & Liu, 2015; Li & Wu, 2004; Turner et al., 1989; Wu et al., 2002) as well as volume 34, issue 9 of Landscape Ecology (Costanza et al., 2019) for more resources. More importantly, they should be cautious about comparing metrics from landscapes described at different scales, or making inferences about landscape patterns beyond the scale of the data used to generate the metrics.

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Choosing at what extent to delineate a sampling area in field studies has critical implications. In a meta-analysis of studies that sampled across multiple extents, Jackson and Fahrig (2015) tested whether effect sizes matched to biologically-­ relevant extents. They found that in most studies, the range of studies did not include the true scale of effect, and that most extents chosen for sampling did not match to biologically-relevant measures such as home range or dispersal distance (Jackson & Fahrig, 2015). In a related study, Moraga et al. (2019) showed that the scale of effect in a study of the wood frog differed depending on whether the response metric was occurrence, abundance or fecundity. A possible solution is to use data across scales, although Martin and Fahrig (2012) showed that, at least for their three mammal study species, multi-scale models did not perform better than single-scale models. Scale consideration is also important in manipulative experiments. In a study of nitrogen (N) enrichment effects on plant diversity, Chalcraft et al. (2008) showed that most studies are conducted on small plots and that at this scale, nitrogen addition decreases plant diversity. However, when they analysed within-plot and among-­ plot data from 18 N-enrichment experiments across North America, they found different effects of nitrogen on biodiversity both at local extents (due to variation in site productivity) and at regional extents. Specifically, in some cases, N-enrichment increased beta-diversity at regional extents, which runs counter to the assumption that N-enrichment always affects diversity negatively. In a similar analysis, but one that leveraged the long-term Park Grass experiments at Rothamstad, Crawley et al. (2005) showed that the mechanisms that influence species richness are scaled. At local scales, interactions between plants, pests and microbes drive plant diversity patterns, while at regional and geographic scales, primary productivity correlates with diversity. Thus, researchers need to be mindful of the fact that mechanisms linking spatial pattern and process operate at different scales. Experiments testing for mechanisms at the wrong scale may fail to detect an effect or detect contradictory findings across scales (Dixon Hamil et al., 2016). These misunderstandings of key drivers may have severe consequences if conservation, management, or land-­ use decisions are based on such incorrect or incomplete information, or if the scale at which the management activity operates differs from the one analysed in the experiment (Sodhi et al., 2011). Hewitt et al. (2007) suggested that the ability for extrapolation from manipulative experiments across scales depended in part on the complexity of the system, and that inference strength across scales was weaker in more complex systems. There are generalizable “rules” about how a change in scale affects analysis; these were first articulated by Meentemeyer and Box (1987). As the size of study area (landscape extent) increases, the level of detail that the observer can discern decreases (that is, you notice more detail about the plants in a meadow when standing in a field than when perched on a nearby mountain looking down a few hundred metres at it). As well, the ability for experimental manipulation or the number of factors that the researcher can consider in an observational study declines with increasing spatial extent. There is a trade-off between the ability to manipulate a system experimentally with the ability to have realism. Small-scale experiments risk having a reductionist view of what are complex landscape systems, and

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examining processes at larger scales can facilitate the detection of emergent system properties (Larsen et al., 2016; Meentemeyer & Box, 1987; Newman et al., 2019; Stewart et  al., 2014). Thus when designing an experiment, the researcher should give thought to what their main goals are. If the goal is detailed understanding of a particular mechanism, perhaps data collection or experimentation at a finer scale is more appropriate. On the other hand, if the goal is a broad systems-level understanding of a landscape, then perhaps a larger scale study is necessary.

5.4  W  hat Can We Learn Through Incorporating Scale into Experiments in Landscape Ecology? To carry out experiments successfully in landscape ecology, researchers need to be aware of scale. I have outlined some of the main considerations above: the scale-­ dependency of many pattern metrics used in observational experiments, and some of the trade-offs with detail vs. realism. Experimental work in the physical sciences often works across scales. For example, engineers test building and bridge stability with models in wind tunnels before building the real thing. They build the scaled-­ down models so all the features are in proportion to each other. The mathematical scaling of the physical features and phenomena means that when the system is scaled-up to the real world, there is a high degree of certainty about the structural integrity of the building or bridge. Unfortunately, ecological processes do not scale up or down as neatly as physical ones (Schneider et al., 1997). However, landscape ecologists are trying to develop scaling rules based on an understanding of the hierarchical structure of landscapes (Denny & Helmuth, 2018; Newman et al., 2019; Urban, 2005; Wu, 1999). Just as an engineering problem starts with wind tunnel experiments, a landscape ecology research question could begin at finer scales; perhaps with highly manipulated mesocosm experiments (Chap. 8). Such experiments “scale down” spatial patch pattern and experimentally manipulate the factor of interest, just as model bridges and buildings are scale replica of the real world. For example, Wiens and Milne (1989) manipulated connectivity and patch configuration in mesocosms to see how beetles respond. They suggested that the results from their mesocosm studies could then be “scaled up” to help understand similar patterns at larger spatial extents. However, unlike model buildings, which scale mathematically to the real world, the mesocosms built by Wiens and Milne (1989) are simplified versions of the real world. We know from hierarchy theory that ecological patterns and processes are complex, such that the processes that influence pattern at one scale are different from at another. This makes it more challenging to design realistic mesocosms, or to extrapolate inferences from elegantly designed mesocosms up to larger extents, since 1:1 scaling rules may not always apply (Schneider et al., 1997). Although scaling up from mesocosms was proposed by Wiens and Milne (1989) over three decades ago, there has been limited success implementing such a

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strategy. Rhode (2019) found that spatial scaling laws are not universal. Newman et  al. (2019) identified three factors that contribute to this difficulty. The first of these is the difficulty of aggregating fine-scale information to larger scales without introducing statistical bias, which they refer to as “coarse-graining”. Ecologists are familiar with coarse-graining data, for example, when they summarize data on individuals at the population level, or collect a suite of water samples in different parts of a lake and average the values across the lake. In experimental design, a key consideration to avoid coarse-graining is to sample at the grain at which the research problem is relevant. Otherwise, information (particularly about variance and distribution) risks being lost as one averages across samples. This can introduce statistical biases and result in spurious inferences (Kennedy & Prichard, 2017). If it is not possible to sample at the same grain that the question is relevant (for example, when using remotely sensed data), then choosing variables that do not change over scales can help avoid the problem. Examples of these are energy (e.g., measured in terms of net productivity) or amount or stoichiometric ratio of atoms like carbon (Newman et al., 2019). The second issue identified by Newman et al. (2019) is what they call the “middle-number” problem, which describes complex landscape systems with too many variables to model easily but too few to make averaging a meaningful solution. They describe how predicting species richness across a region or a landscape is a middle number problem. A host of small-scale habitat and environmental factors controls species occurrence. These can not be meaningfully averaged, but developing a accurate model requires too many variables to be practical (Newman et al., 2019). Another domain of landscape ecology where the middle-number problem is particularly germane is fire forecasting (e.g., Littell et al., 2018). The third factor that makes development of scaling rules difficult is the fact that modelled relationships in landscapes tend not to project well into future environments or into other spaces. This is due to the non-stationarity of landscape data (Newman et al., 2019). In modelling, non-stationarity refers to stochastic processes. Non-stationary processes are those where the means, variance and co-variances change over time— often in unpredictable, stochastic ways. In landscapes, the spatial- and/or temporal-­ autocorrelation of the empirical data used to make predictions violates the assumption that the mean-variance of the data are the same at a different point in time or space. Without meeting this assumption, predictive modelling becomes more challenging. Newman et al. (2019) provide several approaches for modelling complex landscapes that can address all three of these problems (coarse-graining, the middle-­ number problem, and non-stationarity). Across discrete spatial scales (e.g., tree-stand-forest region), Newman et al. (2019) recommend drawing on hierarchy theory and leveraging the hierarchical patch dynamics (HPD) paradigm. The major elements of HPD paradigm are summarized by Wu and Loucks (1995). This dense paper is worth taking the time to digest. The key points of the HPD paradigm are that: (1) ecological systems are viewed as hierarchical systems of patches; (2) broader-scale system dynamics emerge from finer-scale patch dynamics; (3) there are links between pattern and process that occur across a wide range of scales; (4) nonequilibrium perspectives and stochastic processes are accommodated and; (5)

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lower-level processes may create the appearance of stability (a quasi-equilibrium) at higher levels (Wu & Loucks, 1995). Landscape ecologists who are designing experiments in a system that consists of a nested, hierarchical patch-mosaic structure, where the patch dynamics combine to influence system dynamics, might consider explicitly designing their experiments within the HPD framework. If a landscape ecology experiment is occurring along continuous scales (e.g., models of forest fire spread, rather than individual fire patches), then Newman et al. (2019) recommend borrowing cross-scaling tools from disciplines such as physics and advanced computing. These include the use of lacunarity metrics, consideration of which components of the landscape are amenable to scaling, and adopting theoretical frameworks from macroecology. Lacunarity is a different way of characterizing a landscape than the HPD patch-mosaic model. Lacunarity is a metric that counts the presence or absence of a particular feature (e.g., a particular patch type) within a given moving window. The metric is dimensionless, and provides a way to quantify the spatial pattern in a way that is comparable across scales (Dale, 2000) and can be used to choose the scale at which modelling is most appropriate (see Holland et al., 2009 for an example of using lacunarity to assess scale effects in a simulated landscape). Understanding the lacunarity of a landscape at one scale can help to extrapolate a finding up or down to different scales or compare processes across scales. For example, Sung et al. (2019) examined causes of forest fragmentation across different scales and through time in the Korean DMZ. The lacunarity metric allowed them to asses the impact of small-scale processes such as gap-filling as a result of restricted human access, vs. large-scale processes such as development of an industrial zone. Newman et al. (2019) suggested that only certain components of the landscape are amenable to scaling up (or down). They suggest energy as a useful common “currency” for landscape-scale fire modelling. Because energy is measured in the same units across scales, and behaves predictably at all scales, Newman et al. (2019) suggest that it can be usefully applied across a scale continuum. Other abiotic features, such as elements, may also scale well and have been incorporated in landscape-­ scale views of ecosystems (Leroux et  al., 2017, 2020). Across scales, Lan et  al. (2015) carried out a rigorous 10-year manipulative experiment of scale dependence on the effect of nitrogen on species richness. They experimentally added N (at six levels) to 54 5 × 5 m plots using a randomized block design and measured species richness. Their data showed a decrease in species richness with additional N across sampling extents and that the proportional loss of species richness could be modelled (Lan et al., 2015). These results were consistent with those of Crawley et al. (2005) and Chalcraft et al. (2008) which are discussed in the preceding section and which also focused on elements across scales. Other features, such as distribution of individual organisms, do not appear to scale as well, and thus, the scale of sampling and analysis should match the perspective of the organism as best as possible. Despite the lack of clear universal scaling rules, many landscape ecologists suggest there is utility in scaling between and across experiments. In a special issue of Landscape Ecology (vol. 31(1)) on MacroSystems Biology, Gholz and Blood (2016) suggested that a “macro systems” lens was needed to coordinate research that linked

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local ecological processes to broader scale global ones. This echoes Newman et al.’s (2019) recommendation to consider perspectives from macroecology to address some of the challenges of scaling. The special issue summarized research from integrated US-wide networks such as the Long-Term Ecological Research (LTER) Program and the National Ecological Observational Network (NEON). For example, Hall et al. (2016) examined microclimate patterns in residential areas across the United States to assess whether and how urban heat island patterns differ across broad climate regions of the United States. They found that residential microclimates were more similar among each other in the morning hours, but that regional climate contexts had an influence on daily and seasonal variation in microclimates. Similarities in landscape structure yielded convergence in microclimate patterns, suggesting strategies for universal design of residential neighbourhoods that could help alleviate climate change effects. There have been examples of studies that successfully “scale up” from plot-level data to regional extents. Jiang et al. (2016) (included in the special issue on macrosystems ecology in Landscape Ecology) successfully used plot-scale measures of soil C, N and P to develop models that extended across the North Slope of Alaska. Their models for vegetation cover, C stocks and biomass closely matched observed values (at a 1 × 1 km spatial resolution). However, how well these models will perform under climate change is not known; non-stationarity (Newman et al., 2019) suggests that there are good reasons to be uncertain. In addition, Jiang et al. (2016) identified ecological and biological processes specific to the Alaska environment which might contribute to model uncertainty. This linkage of real-world mechanisms to an understanding of model performance is a hallmark of successful modelling. Scaling issues also apply to models that take fine-grain, small extent data (either collected in the real world, or themselves generated in a simulation) and extrapolate these to larger scales via modelling approaches. Urban (2005) emphasized the importance of scaling ecological processes rather than patterns. This is directly relevant to experimental work in landscape ecology, since well-designed experiments should help us to infer the processes that create the observed patterns. Although Urban (2005) notes that simple models such as species-area relationships, or logistic population growth can be useful for describing many ecological processes, these become more complex as soon as they are spatially explicit. Dixon Hamil et  al. (2016) emphasize that ignoring spatial heterogeneity can lead to uncertainties when relationships are modelled across spatial scales. The unique features of landscapes—their nonlinearity and complexity—make modelling (and experimentation) more challenging to carry out. Models seek to simplify the real world, but can do so at the expense of model utility. Highly realistic models or experiments may be accurate, but not useful for long-term prediction or extrapolation. When collecting data to use in models to extrapolate across scales, researchers must take into account how they collect and analyse data. The ways data are collected in population or community ecology studies (often focused on sampling within a patch) may not work for a landscape study where scale and spatial heterogeneity are key attributes.

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There are numerous solutions to these problems, and this book aims to highlight some of them. Consideration of scale a priori (the topic of this chapter) is an important step. Hewitt et al. (2007) provide a useful decision tree for considering how scale effects influence experimental design. Thinking about sampling design (Chap. 4) is also important. Careful choice of the modelling/statistical tools can also be a factor. For example, Dixon Hamil et al. (2016) suggest mixed effects models can address multi-scaling issues, but this is not the only solution. As well, specific considerations for experimental design that capture the unique aspects of landscapes can help to improve inference across scales.

5.5  The Bottom Line Landscape ecologists seeking to do experiments without considering scale effects do so at their peril. In particular, studies that are explicitly designed to scale up or down should consider how to address the issues of coarse-graining, the middle-­ number problem, and non-stationarity (Newman et al., 2019) in addition to all the other attributes of landscapes (thresholds, nonlinearities, time lags, and neighbourhood influences) that make them interesting, not to mention challenging to experiment on (Urban, 2005)! Without considering how the grain and extent of sampling affect the research outcome, inferences might only be limited to that single study, which is not the way the scientific method ideally works (see Chap. 2). Researchers should strive to do sampling and/or manipulations at the scale that matches the process they are interested in, or consider the scale at which their target organism operates (Jackson & Fahrig, 2015; Kleijn et al., 2018; Kotliar & Wiens, 1990; Moraga et al., 2019; Wiens & Milne, 1989). They should test how scaling-up affects their data and the inferences made to assess how far they can make inferences across scales. This is particularly important if the scale at which decisions are made, or at which management is implemented is different from the scale at which the research is conducted (Sodhi et al., 2011; Urban, 2005). Finally, despite the massive literature on scale in our discipline, it is important to remind emerging researchers that we are not “done” with scale. Scale in and of itself is a concept that can be the focus of research. Meentemeyer and Box (1987) list nearly two-dozen scale related hypotheses (see Tables 2.7 and 2.8  in their book chapter). Many of these research questions have not been resolved, and indeed, in their “think tank” with leading landscape ecologists at the 2001 conference in Arizona, Wu and Hobbs (2002) listed “scale” as one of the top 10 research topics for landscape ecologists. Despite being obsessed with scale since the earliest days of the discipline and with numerous papers about landscape scale in existence (Wiens et  al., 2007; Wu, 2017), it appears that scale issues are still a fruitful area for research. To advance the discipline further, researchers need to assess scale effects through careful and rigorous experiments.

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Box 5.1: Key Definitions and Concepts of Scale Extent: The overall area encompassed by the study (Wiens, 1989); the largest scale of heterogeneity to which an organism responds (from Kotliar & Wiens, 1990) Fractal dimension:A measure of the statistical complexity in a geometric shape. The index D is a non-integer that measures between 1 and 2 and allows for a comparison of how the details of a geometric pattern change with the scale at which the pattern is measured. For example, the length of a coastline of a given geographic feature increases as the scale of the measuring unit decreases (from Mandelbrot, 1983) Grain: The size of the individual units of observation (Wiens, 1989); the smallest scale at which an organism responds to the pattern of patches on the landscape (i.e., to patch structure; from Kotliar & Wiens, 1990) Hierarchical structure: Describes how a biological system is composed of interacting components (i.e., lower-level entities) and is itself a component of a larger system (i.e., higher-level entities) (from O’Neill et al., 1989) Landscape: An area that is spatially heterogeneous in at least one factor of interest; a spatial mosaic of patches (from Forman & Godron, 1981) Patch: A defined area that is homogenous in one or more characteristics (e.g., land cover, stand age, soil type) relative to the surrounding area (from Forman & Godron, 1981) Scale: We can describe the concept of “scale” verbally, graphically, and mathematically. There are different types and measurements of scale (e.g., temporal, cartographic); the definition germane to landscape ecology is that “scale refers to the extent relative to the grain of a variable in time or space” (Schneider, 2001a, b). Scale of effect: The spatial extent at which the measured landscape structure best predicts the response of interest (from Jackson & Fahrig, 2015) Scaling rules: Also known as scaling laws. An approach in which patch hierarchies are used to simplify the complexity of system under study, enhance ecological understanding, and minimize the danger of intolerable error propagation in translating information across multiple scales (from Wu, 1999) Spatial composition: The variety and abundance of patch types within a landscape (from McGarigal & Marks, 1995) Spatial configuration: The physical distribution of spatial character of patches within the landscape (from McGarigal & Marks, 1995)

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Moraga, A. D., Martin, A. E., & Fahrig, L. (2019). The scale of effect of landscape context varies with the species’ response variable measured. Landscape Ecology, 34, 703–715. https://doi. org/10.1007/s10980-­019-­00808-­9 Newman, E.  A., Kennedy, M.  C., Falk, D.  A., & McKenzie, D. (2019). Scaling and complexity in landscape ecology. Frontiers in Ecology and Evolution, 7, 293. https://doi.org/10.3389/ fevo.2019.00293 O’Neill, R. V., Johnson, A. R., & King, A. W. (1989). A hierarchical framework for the analysis of scale. Landscape Ecology, 3, 193–205. https://doi.org/10.1007/BF00131538 Pattee, H. (1973). Hierarchy theory, the challenge of complex systems. George Braziller. Pittman, S. J., Wiens, J. A., Wu, J., & Urban, D. L. (2018). Landscape ecologists’ perspectives on seascape ecology. In S. J. Pittman (Ed.), Seascape ecology (pp. 485–492). Wiley Blackwell. Rhode, K. (2019). Spatial scaling laws may not apply to most animal species. Oikos, 93, 499–504. Schneider, D. C. (2001a). The rise of the concept of scale in ecology. BioScience, 51, 545–554. Schneider, D. C. (2001b). Scale, concept and effects of. Encycl Biodivers, 5, 245–254. Schneider, D. C., Walters, R., Thrush, S., & Dayton, P. (1997). Scale-up of ecological experiments: Density variation in the mobile bivalve Macomoa liliana. Journal of Experimental Marine Biology and Ecology, 216, 129–152. Sodhi, N. S., Butler, R., Laurance, W. F., & Gibson, L. (2011). Conservation successes at micro-, meso- and macroscales. Trends in Ecology & Evolution, 26, 585–594. https://doi.org/10.1016/j. tree.2011.07.002 Staveley, T. A. B., Hervall, P., Stjärnkvist, et al. (2020). Exploring seagrass fish assemblages in relation to the habitat patch mosaic in the brackish Baltic Sea. Marine Biodiversity, 50, 1. Stewart, J., Parsons, A. J., Wainwright, J., et al. (2014). Modeling emergent patterns of dynamic desert ecosystems. Ecological Monographs, 84, 373–410. Sung, C. Y., Park, C.-B., & Kim, J.-S. (2019). Politics of forest fragmentation: A multiscale analysis on the change in the structure of forest landscape in the North and South Korean border region. Regional Environmental Change, 19, 137–147. https://doi.org/10.1007/s10113-­018-­1394-­7 Turner, M. G., & Romme, W. H. (1994). Landscape dynamics in crown fire ecosystems. Landscape Ecology, 9, 59–77. Turner, M. G., O’Neill, R. V., Gardner, R. H., & Milne, B. T. (1989). Effects of changing spatial scale on the analysis of landscape pattern. Landscape Ecology, 3, 153–162. https://doi. org/10.1007/BF00131534 Urban, D.  L. (2005). Modeling ecological processes across scales. Ecology, 86, 1996–2006. https://doi.org/10.1890/04-­0918 Urban, D. L., O’Neill, R. V., & Shugart, H. H. (1987). Landscape ecology: A hierarchical perspective can help scientists understand spatial patterns. Landscape Ecology, 37, 119–127. Vance, T.  C., & Doel, R.  E. (2010). Graphical methods and cold war scientific practice: The Stommel diagram’s intriguing journey from the physical to the biological environmental sciences. Historical Studies in the Natural Sciences, 40, 1–47. https://doi.org/10.1525/ hsns.2010.40.1.1 Wiens, J.  A. (1989). Spatial scaling in ecology. Functional Ecology, 3, 385–397. https://doi. org/10.2307/2389612 Wiens, J. A., & Milne, B. T. (1989). Scaling of “landscapes” in landscape ecology, or, landscape ecology from a beetle’s perspective. Landscape Ecology, 3, 87–96. https://doi.org/10.1007/ BF00131172 Wiens, J. A., Moss, M. R., Turner, M. G., & Mladenoff, D. J. (2007). The central role of scale. In J. A. Wiens, M. R. Moss, M. G. Turner, & D. J. Mladenoff (Eds.), Foundation papers in landscape ecology (pp. 287–290). Columbia University Press. Winemiller, K. O., Flecker, A. S., & Hoeinghaus, D. J. (2010). Patch dynamics and environmental heterogeneity in lotic ecosystems. Journal of the North American Benthological Society, 29, 84–99. With, K.  A. (1994). Using fractal analysis to assess how species perceive landscape structure. Landscape Ecology, 9, 25–36. https://doi.org/10.1007/BF00135076

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With, K. A., Cadaret, S. J., & Davis, C. (1999). Movement responses to patch structure in experimental fractal landscapes. Ecology, 80, 1340–1353. https://doi.org/10.1890/0012-­9658(199 9)080[1340:MRTPSI]2.0.CO;2 Wu, J. (1999). Hierarchy and scaling: Extrapolating information along a scaling ladder. Canadian Journal of Remote Sensing, 25, 367–380. https://doi.org/10.1080/07038992.1999.10874736 Wu, J. (2004). Effects of changing scale on landscape pattern analysis: Scaling relations. Landscape Ecology, 19, 125–138. https://doi.org/10.1023/B:LAND.0000021711.40074.ae Wu, J. (2017). Thirty years of landscape ecology (1987–2017): Retrospects and prospects. Landscape Ecology, 32, 2225–2239. https://doi.org/10.1007/s10980-­017-­0594-­8 Wu, J., & Hobbs, R. (2002). Key issues and research priorities in landscape ecology: An idiosyncratic synthesis. Landscape Ecology, 17, 355–365. https://doi.org/10.1023/A:1020561630963 Wu, J., & Loucks, O. L. (1995). From balance of nature to hierarchical patch dynamics: A paradigm shift in ecology. The Quarterly Review of Biology, 70, 439–466. https://doi.org/10.1086/419172 Wu, J., Shen, W., Sun, W., & Tueller, P.  T. (2002). Empirical patterns of the effects of changing scale on landscape metrics. Landscape Ecology, 17, 761–782. https://doi.org/10.102 3/A:1022995922992

Part II

Approaches to Experimentation

Chapter 6

Large-Scale Manipulative Experiments

6.1  What Are Large-Scale Manipulative Experiments? For the purposes of this book, I am defining large-scale manipulative experiments as manipulative experiments (as opposed to observational or “natural” experiments; see Chap. 2 for the distinction between the two) that occur over large spatial extents and under natural conditions. What defines “large extent” is an arbitrary threshold, but for the sake of this book, I am going to define any study that has a spatial extent of more than 15 hectares (ha) as a large-extent study. If you have trouble visualizing area, an American football field is approximately half a hectare (0.44 ha to be exact) and an international soccer pitch is just over ¾ of a hectare (0.825 ha to be exact). Thus, my minimum size criteria for a large-extent study is one that is at least as big as 34 American football fields or 18 soccer pitches. I am partly basing this cut-off on the distinction between the maximum size of highly manipulated experiments that are semi-natural (I am thinking of intensive experimental systems like the Bowling Green Experimental System, which is 4  ha) and those that manipulate aspects of the landscape less intensively—for example that are embedded in a more natural matrix (such as the Savannah River project (Fig. 6.1) discussed below). I will discuss these more intensive/highly manipulated, semi-natural experiments (what I am calling “experimental model landscapes”) in the next chapter. In this chapter I focus on experiments in forest, grassland and aquatic systems that have carried out manipulations at large extents, and which address landscape ecology questions that fit one or more of the experiment types described by Jenerette and Shen (2012). A number of the experiments discussed here are included in a review by Fayle et  al. (2015) on “whole-ecosystem experimental manipulations”; others described by Fayle et al. (2015)—while interesting and elegant experiments—are focused more on community- or ecosystem-level questions, rather than landscape ecology ones. In a large-scale manipulative experiment, the researcher is actively manipulating one aspect of the landscape (for example, either the ecological pattern or an © Springer Nature Switzerland AG 2022 Y. F. Wiersma, Experimental Landscape Ecology, Landscape Series 29, https://doi.org/10.1007/978-3-030-95189-4_6

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Fig. 6.1  Aerial image of one replicate of the experimental design at the Savannah River site. The patch in the foreground, labelled “unconnected rectangular” is 100  ×  100  m. Photo by Ellen Damschen (2013) Landscape Corridors, in Encyclopedia of Biodiversity, second edition with permission from Elsevier

ecological process) to test a hypothesis. Because these experiments happen in natural systems, background ecological processes remain intact. This aspect of largescale manipulative experiments allows for a high degree of realism. Experiments done in a natural landscape setting, such as the ones that are the focus of this chapter, focus on isolating one phenomenon to assess how the system responds. This approach can provide the researcher with more realistic inferences about how the natural world functions than a lab-based experiment, which managers in turn can use to apply decisions and policies for natural resources and landscape management (Mayer et al., 2016). In terms of meeting the criteria for a good experimental design as outlined in Chap. 2 (control, replication, randomization), having a control is usually quite straightforward in large-scale experiments. I will discuss a few examples of large-­ scale experiments below to illustrate how to do this. Randomization is often not difficult to apply, although an understanding of the underlying pattern of a given landscape may be necessary, and the researcher may need to apply strategies such as a stratified random sampling design to increase inferential power. Replication is more difficult. The spatial extent of these types of experiments is such that it can be difficult to have multiple replicates, if any. Many of the examples I will discuss in

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this chapter have replicate treatments, but the number of replicates is usually quite low in large-scale experiments, compared to an experiment in a lab setting. Researchers have used large-scale experiments for many different purposes. In terms of Jenerette and Shen’s (2012) taxonomy of types of landscape experiments (reproduced in Chap. 3), large-scale experiments are especially amenable to many of the types of experiments that are focused on identification of process variation within landscapes (Group II), identification of process sensitivity to landscape structure (Group III) and identification of landscape pattern formation factors (Group IV). It is less common to see large-scale experiments used for identification of landscape structure (Group I), although there are a few examples. See Table 6.1 for details of which types of experiments within these groups are especially amenable to making use of large-scale experiments.

Table 6.1  Taxonomy of types of landscape experiments (sensu Jenerette & Shen, 2012), with bold font in the example column indicating the type of experiment for which large-scale manipulations are especially-well suited, and italic font for those types which it may be possible to harness large-­ scale manipulations, but for which other experimental approaches may be better suited. References describing examples of large-scale manipulative experiments of each type are given; these are not exhaustive Group I. Identification of landscape structure II. Identification of process variation within landscapes

III. Identification of process sensitivity to landscape structure

Type of experiment 1. Perception experiment 2. Tracer experiments 3. In situ experiments distributed throughout a landscape 4. Ex situ experiments using samples collected throughout a landscape 5. Translocation experiments 6. Transport manipulations 7. Manipulation of internal patch characteristics 8. Manipulation of patch shape 9. Manipulation of patch connectivity 10. Fragmentation experiments

11. Manipulation of landscape scale 12. Construction of entire landscapes IV. Identification of landscape 13. Manipulative disturbances pattern formation factors 14. Vector manipulations

Example Abu Baker and Brown (2010) Tietema et al. (1998) Power et al. (2016)

Valente et al. (2019) Nakano et al. (2018) Groffman and Turner (1995) and Kay et al. (2017) Brinkerhoff et al. (2005) Schmiegelow et al. (1997) and Brinkerhoff et al. (2005) Margules (1992), Schmiegelow et al. (1997) and Rocha et al. (2017)

Concilio et al. (2005) and Wu et al. (2015)

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6.2  Advantages and Disadvantages of Large-Scale Experiments One of the major advantages of large-scale manipulative experiments is their realism. Since they occur in situ, findings from these kinds of experiments are usually more relevant to land managers and practitioners than findings from lab-based experiments or from scaled-down micro/mesocosms. Often large-scale manipulations are designed explicitly to address a management problem, and the experiment is developed under an adaptive management framework (sensu Walters & Holling, 1990). Adaptive management sounds like an easy-to-apply framework, but it is challenging to do well (Westgate et al., 2013). Researchers need to work with practitioners to translate policy objectives carefully into valid and testable research hypotheses. Following this, the management action(s) (for example, forest cutting patterns, wildlife/fish harvest quotas, or agricultural crop rotations) must be applied with as rigorous an experimental design as possible. Replication becomes key here; Walters and Holling (1990) illustrate a hypothetical example of an adaptive management experiment in which having replicate experimental units decreases the probability that the experimental application of a policy will fail. Large-scale experiments also carry with them challenges and disadvantages. Because the experiment is set up in the natural world, it is subject to the vagaries of nature. Unforeseen natural events, like once-in-a-century floods, windstorms, or wildfires, may destroy the experimental set-up, or create conditions within the system that do not represent the “norm”. While such natural disturbances can lead to interesting observational studies that lend insights into how disturbances shape landscapes and ecological processes, the effect of the disturbance on the initial experimental set up may be quite detrimental. Another source of disturbance may be human-caused. Many large-scale manipulative experiments are set up in natural areas used by humans for recreation. Whether deliberately or accidentally, these visitors may disturb or disrupt the experiment to the extent that the results are unreliable. Additionally, because the experimenter does not have full control over the system, as they would in a controlled greenhouse or laboratory setting, it may be difficult to ascertain that observed effects are due to the experimental manipulation and not due to some underlying, and potentially unobserved natural phenomenon. Beyond the risk of experimental failure due to natural or human disturbance, or the difficultly of inferring mechanisms that may not be observable, large-scale experiments have further challenges in that they are usually expensive to set up and maintain. For example, a fact sheet on the Hubbard Brook Experimental Forest (USDA, 2008) lists its annual operating costs at US$320,000 with critical and long-­ term budgetary needs in excess of US$400,000. This is larger than the average research grant given to individual ecologists. Thus, governments or universities often own and/or manage many of the well-known large-scale study field sites that are available for researchers from different institutions or departments to use. While this consolidation of resources and site management has cost efficiencies, it can also make such sites vulnerable to fiscal constraints. When faced with the need to cut

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budgets, these areas may be subject to cut backs, and even complete shut downs (e.g., Hoag, 2012). Finally, because many natural processes occur slowly, the time scale of these large-scale experiments may not match the time limit of many Masters or Doctoral thesis projects, or may not yield major results within the typical 2–5 year period of most grants. Even when a researcher can obtain a result from a large-scale manipulative experiment within the scope of a graduate degree or short-term grant, these results may not be consistent when the experiment extends over longer periods (Haddad et  al., 2015). For example, in the Calling Lake Fragmentation Study, Schmiegelow et al. (1997) found that habitat fragmentation did not affect species richness in the fragmented patches 2 years after experimental harvest, but that there were changes in bird community structure. Longer-term research showed different effects. Over a 24 year period post-harvest, Leston et al. (2018) showed that species responses to landscape fragmentation in these same patches were more complex. They showed that bird communities in this experimental landscape were influenced by changes within harvested patches as they underwent vegetative succession, and, for some species, influences from annual variation in abiotic conditions such as, for example during, El Niño years, also affected their occupancy (Leston et al., 2018).

6.3  Case Examples Researchers have carried out large-scale manipulative experiments in different types of ecosystems. A review of the literature suggests that some types of ecosystems are more amenable to manipulative experiments; thus, I have grouped the case examples by ecosystem type and also described which type of experiment (sensu Jenerette and Shen’s (2012) taxonomy) each best typifies.

6.3.1  Forest Experiments Many of the most ambitious large-scale manipulations have been carried out in forests of all types, from boreal to tropical (e.g., Schmiegelow et al., 1997; Laurance et al., 1998; Craig et al., 2011; Ewers et al., 2011; Rocha et al., 2017). These studies generally experimentally manipulate one or more factors of patch size, shape, and connectivity to assess how these variables affect the presence or abundance of particular organisms, and thus in Jenerette and Shen’s (2012) taxonomy of experiment types, they fall largely within group III (see Table 6.1). Such large-scale manipulations are often financially feasible because the forest harvest carried out to create the experimental patches can yield timber of economic value. Such an approach may also be a way to manipulate patch quality (e.g., Curzon et al., 2017). Indeed, in the Calling Lake Fragmentation Study in northern Alberta, Canada, the project has been carried out over multiple decades through co-operation with a major forest industry

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partner (Schmiegelow et al., 1997; Leston et al., 2018). Similarly, in the Wog Wog Fragmentation Experiment in New South Wales, Australia, researchers took advantage of the conversion of an 80–100 year old Eucalyptus forest to a pine plantation to leave behind experimental fragments (Margules, 1992). In the Stability of Altered Forest Ecosystems (SAFE) project in Malaysian Borneo, the conversion of forest to oil palm plantations was capitalized on to create experimental fragments (Ewers et  al., 2011). Other forest-based landscape experiments manipulate disturbance instead of patch pattern. For example, researchers at the Teakettle Experimental Forest in California carried out a crossed design of two levels of burning (burned/ unburned) and three levels of thinning, (Goodwin et  al., 2018). Conversely, the Missouri Ozark Forest Ecosystem Project (MOFEP) and various other experimental forests in the United States (Curzon et al., 2017) used forest harvest intensity as the manipulation (Gram et al., 2003). The overall extent of these forest-based manipulations varies, as does the experimental treatment (Table 6.2). Even for studies that are similar in their broad question (for example, examining the effects of fragmentation), the size and shape and degree of isolation of the experimental patches varies (see Table 6.2). The amount of effort involved to create and maintain these patches is substantial, so it is not surprising that the experimental replicates are limited. While replication of experimental blocks may seem to be limited in these kinds of studies, compared to other types of experiments, they compensate for this with their longevity. The Calling Lake and Savannah River experiments have been running since the 1990s, and the Biological Dynamics of Forest Fragments Project (BDFFP) since the late 1970s (Table 6.2). With measurements across many years (and with proper allocation of between-years variation to the Mean Square Error and F-ratio, see Chap. 4), statistical rigor can be increased. Moreover, a proper experimental control is quite straightforward to apply in these experiments when the experiment is embedded within natural forests. All of the above studies use patches of intact forest of the same size(s) as the treatment blocks, and interspersed between the experimental fragments as control locations. The implicit assumption in these experiments is that the surrounding matrix is homogenous. Of course, this is not likely to be true. However, the fact that natural processes continue in the area surrounding the experimental patches can yield opportunities for further research into how variation in the matrix affects what happens in the patches. For example, land abandonment by cattle ranchers in the surrounding area of the BDFFP facilitated post hoc analyses of matrix effects (Nascimento et al., 2006). Similarly, the SAFE Project has been designed to allocate replicate experimental blocks along a gradient of different intensities of forest disturbance (Ewers et al., 2011) to assess how these aspects of the matrix affect outcomes within the experimental blocks. Different projects focus on different responses to patch and mosaic patterns, including communities (e.g., Leston et  al., 2018), ecosystem processes (e.g., Laurance et al., 2002), and populations (e.g., Rocha et al., 2017). When focusing on populations, researchers should chose a focal organism whose dispersal ability and home range match the scale of the manipulation. These projects have made use of a

Selective harvest, shelterwood harvest Burning (2 levels: Burned/ unburned) and thinning (3 levels; overstory, understory, none) Forest remnants (3 levels; 1, 10, 100 ha) Clearings in the forest (1.4 ha) – 6–8 Isolated, with “wings”, with corridors Forest remnants (3 levels, 0.25, 6 0.875, 3.062 ha)

1578

80,000

Patch area, isolation and edge Patch isolation and edge

Patch area and isolation

Stability of Altered Forest Ecosystems (SAFE) Savannah River

Wog Wog

20

7200

1300

~3700

Forest remnants (4 levels; 1, 10, 40, 100 ha) Forest management (3 levels; clearcut, selective cut, control)

14,000

1997

1950

1990

1993

1974

1979

Year began 1947

Eucalyptus regrowth forest

1987

2011 Tropical forest surrounded by forest/oil palm plantation Temperate forest 1993

Mixed-conifer

3

6

Mixed-conifer

Oak-pine

Boreal forest

Northern hardwood

Tropical forest

Environment Northern hardwood

3

3

3

3

Patch area and isolation Forest management

Selective harvest, clearcut

1052

1–5

Treatment Replicates 9

Silviculture

Treatments Crop tree release; light and heavy selective harvest Forest remnants (4 levels, 1, 10, 100, 200 ha)

16,000

Extent (ha) 2630

Patch area and edge

Manipulation Silviculture

Missouri Ozark Forest Ecosystem Project (MOFEP) Penobscot Silviculture Experimental Forest Teakettle Experimental Burning and Area thinning

Experiment name Argonne Experimental Forest Biological Dynamics of Forest Fragments Project (BDFFP) Bartlett Experimental Forest Calling Lake

Table 6.2  Comparison of experimental designs of the large-scale fragmentation experiments discussed in this chapter

Margules (1992)

Brinkerhoff et al. (2005)

Ewers et al. (2011)

Curzon et al. (2017) Goodwin et al. (2018)

Curzon et al. (2017) Schmiegelow et al. (1997) Gram et al. (2003)

References Curzon et al. (2017) Bierregaard et al. (1992)

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variety of focal species. Schmiegelow et al. (1997) used point-counts of song birds, which is a well-established method for bird surveys that has successfully been used annually at this site for over two decades (Leston et al., 2018). The BDFFP project has used also used birds as the focal organism (e Silva, 2013; Rutt et al., 2017) as well as looking at the effects of the experimental fragments on bats (Rocha et al., 2017; Sampaio et al., 2003) and non-volant mammals (Stone et al., 2009) including primates (Boyle et al., 2009; Boyle & Smith, 2010). At the SAFE site, Deere et al. (2020) used 74 camera traps distributed across the landscape to assess how seven different mammals responded to different habitat types created through the fragmentation process. The Savannah River site has used the experimental fragments to study a range of taxonomic responses (see summary in Haddad et al., 2003), including birds (Evans et al., 2013), small mammals (Brinkerhoff et al., 2005; Danielson & Hubbard, 2000) and arthropods (e.g., Haddad & Tewksbury, 2005; Orrock et al., 2011). The longevity of many of these experiments has also helped to develop an understanding of the processes of survival, reproduction, and dispersal on species biodiversity patterns in fragmented landscapes (Haddad et al., 2015; Laurance et al., 2011) and in response to disturbance both immediately following, and several years after the event (Goodwin et al., 2018). The Savannah River site has also been used to experimentally test how fragments and patch pattern affect ecological processes such as fire (Brudvig et al., 2012), seed predation (Craig et al., 2011), seed dispersal (Damschen et al., 2014), and fungal pathogens (Johnson & Haddad, 2011). In addition to testing how ecological processes respond to patch shape and connectivity/fragmentation using these manipulations (experiment Types III.8, III.9 and III.10 in Jenerette & Shen, 2012), some of the research at these sites has distributed experiments within the landscape to test different types of questions. For example, Craig et  al. (2011) distributed seed removal depots around the experimental clearings at the Savannah River site to assess how fragmentation affected seed predation. This is an example of a distributed in situ experiment to identify process variation (Type II.3 in Jenerette & Shen, 2012). In the SAFE project, several studies have examined how the level of disturbance within the fragments themselves, rather than the patch configuration, affected functional diversity of ants and termites (Luke et al., 2014), detection of several species of rodent (Cusack et al., 2015) and primate species richness (Bernard et al., 2016). Although the actual within-patch manipulation is minimal, these studies serve as examples of experiments that examine how internal patch characteristics (Type III.7 in Jenerette & Shen, 2012) affect ecological patterns and processes. Other projects, such as the Teakettle Experiment Forest and the MOFEP manipulated patch characteristics more explicitly through burning, harvest or thinning (Gram et al. 2003; Goodwin et al., 2018). These latter studies have investigated how different types and levels of disturbance affect a host of different forest ecological components, including birds (e.g., Gram et al. 2003); mammals (e.g., Frantz & Renken, 2005), forest understory vegetation (e.g., Goodwin et al., 2018), and soil respiration (Concilio et al., 2005). Other experiments have looked at different aspects of the landscape pattern. In a study in an experimental forest in Japan, Nakano et al. (2018) used experimental playbacks of vehicle noise to assess how noise affected the probability of frogs

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crossing gaps with different cover types. A similar manipulation at the Savannah River site used roads closed to the public to experiment with how the approach of a car along a road affected the probability of different species of snakes to cross (Andrews & Gibbons, 2005). Both of these are examples of transport manipulations (experiment Type II.6 in Jenerette & Shen, 2012) which introduce a manipulation to reduce movement of a target organism. Most of the experiments mentioned thus far manipulate landscape pattern. However, there are large-scale experiments in forest systems with different kinds of manipulations. Tracer experiments (Type I.2 in Jenerette & Shen, 2012) release a known quantity of a substance (e.g., fertilizer; Tietema et al., 1998) or object (e.g., model spores; Allen et al., 1989) into a landscape and assess the impact it has on the system or the way the landscape configuration affects the focal object’s dispersal. Translocation experiments (Type II.5 in Jenerette and Shen (2012) are those where an element of one landscape is moved to another to assess how the organism or feature responds to the difference between their landscape of origin and the novel landscape. For example, Valente et al. (2019) translocated 36 wood thrushes and 19 oven birds between two sites that differed in the degree of forest fragmentation (created through natural processes). They monitored movement of individuals using telemetry to test how forest loss and forest fragmentation affect movement. In a similar experiment Castellón and Sieving (2006) translocated an understory bird between three different landscape configurations to test how landscape permeability (measured as the relative composition of forest to shrubby vegetation to open patches) affected its movement. Goheen et al. (2003) carried out a translocation in a similar forest-agricultural matrix, but using radio-collared squirrels. These studies all illustrate the limitation of translocation experiments; they are species-specific and thus cannot make broader inferences about how landscape pattern affects processes such as functional connectivity (Betts et al., 2015). Forest ecosystems have been shown to be amenable to large-scale experiments, especially those related to landscape structure, largely because ongoing land management activities can successfully be harnessed to the service of well-designed experiments (Curzon et al., 2017; Ewers et al., 2011; Margules, 1992; Schmiegelow et al., 1997). One major caveat is that many of these experiments have been grounded in the patch-mosaic model and have assumed that species responses are due to the fragmentation process, and not the habitat loss on its own. Disentangling the effects of habitat loss and fragmentation can be tricky (Fahrig, 1997, 2013; Jackson & Fahrig, 2016), and the scale of the experimental systems described in this study make it difficult to have enough space for the level of replication that would be necessary to tease out the relative effects of these two processes. In the next chapter, I will show how experimental model landscapes, at a smaller extent than those discussed here, can achieve an experimental design to address this. Finally, understanding how the variation in the surrounding matrix influences the manipulated patches requires further careful analysis. In forest systems, the response of organisms and ecological processes to the experimental fragmentation can occur slowly. Large-scale experimenst in ecosystems with more dynamic processes, as we

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will see in the next section, can address some of these temporal limitations that forested systems offer.

6.3.2  Grassland Experiments With their open habitat dominated by grasses and other non-woody plants, grassland ecosystems serve as good systems for manipulative large-scale experiments. They have an advantage over forests in that the plant species within them tend to grow faster than trees, and thus it can be easier to see a response over a shorter period. As with forest systems, many of the large-scale experiments have harnessed human use and management (grazing, agriculture) in an experimental fashion in their project (e.g., Kay et al., 2017; Wan et al., 2015; Wu et al., 2015). Also similar to the forested landscape examples, many studies occur on large-scale grasslands controlled by university or government research institutes (e.g., the Konza Prairie Biological Station run by Kansas State University or the Inner Mongolia Grassland Ecosystem Research Station run by the Chinese Academy of Sciences). Grassland experiments seem to be highly amenable to examining the links between landscape patterns and ecological processes, perhaps more so than forest experiments. The Inner Mongolian Grassland Removal Experiment (IMGRE) was established in 2006 and is focused on making links between biodiversity and ecosystem function across scales (Wu et al., 2015). This large study consists of 8 replicate blocks, each divided into 96 plots (6 × 6 m). The manipulations involve partial or complete removal of targeted plant functional groups (Wu et  al., 2015; Yuan et  al., 2015). In a second experiment, researchers treated a subset of plots with experimental grazing by either caged grasshoppers or controlled sheep herding (Wan et  al., 2015). In both cases (experimental plant removal and experimental grazing), the goal was to assess the impact of these disturbances on ecosystem function (Yuan et al., 2015). The team measured ecosystem function using a variety of metrics, including plant composition, biomass, litter decomposition, and soil/plant elemental composition and ratios (carbon, nitrogen, phosphorous). The rapid growth of grassland flora compared to trees allows for tests that manipulate the internal patch characteristics more easily than in forest systems (experiment Type III.7 in Jenerette & Shen, 2012). For example, Kay et al. (2017) carried out a replicated grazing experiment over a 15,000  km2 area in Australia, which combined a natural experiment (experimental blocks stratified by past grazing practices) with a manipulative experiment (grazing exclusion via fences vs. varying levels of grazing) to assess the impact of  sheep grazing activity on herpetofauna richness and composition. At the Konza Prairie Research Natural Area in Kansas, Groffman and Turner (1995) took advantage of different within-patch treatments (burning vs. grazing) and a control at nine sites within a 15 × 15 km region. Their focus was on interpreting remotely-sensed data from these manipulated patches to assess plant productivity and how this related to nitrogen flux as measured in situ with soil cores (Groffman & Turner, 1995). The fully replicated burning/grazing

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manipulations of the patches at Konza have been used for a variety of studies in ecosystem and landscape ecology (Knapp et  al., 1998), including assessment of how disturbance shapes spatial heterogeneity in forage quality (Raynor et al., 2015). Grasslands around the world are one of the most productive biomes, but they do not always respond the same way to disturbances. Thus, research that integrates findings from across these different large-scale experiments is necessary. For example, Koerner and Collins (2013) contrasted data from the Konza Prairie Research Area with data from the Experimental Burn Plots (EBPs) in African Grasslands in Kruger and found that fire and grazing impact patch structure differently on the two continents. Grassland systems have also proven to be amenable to distributed experiments (experiment Type II.3 in Jenerette & Shen, 2012). Although at a little smaller extent than the threshold for this chapter, the DRI-Grass (Drought and Root Herbivore Impacts in a Grassland) experiment in Australia is a good example of a distributed experiment. In this study, the researchers use experimental rainfall shelters (2 × 2 m in size) that manipulate different levels of drought/rainfall, which they distribute across the field in a randomized design. In addition, the researchers are examining the impacts of root herbivory on plant productivity through experimental additions of different levels of soil herbivore (scarab beetles) to the plots. There are six replicates of each combination of treatment levels (Power et al., 2016). At a larger extent, the EDGE (Extreme Drought in the Grasslands Experiment) is a similar type of experimental manipulation, that distributes larger rainfall shelters across 6 grassland sites in the central United States (see Web Supplemental Information in Levy et al., 2014). As with the DRI-Grass experiment, the response variables in the EDGE experiment focus on above- and below-ground productivity. Other distributed experiments in grassland systems have taken advantage of the natural pattern of forest patches interspersed within the grassland to set up distributed experiments. For example, in South Africa, Abu Baker and Brown (2010) used the woody patches (averaging 500 m2 in area) surrounded by grasslands to set up giving-up-density (GUD) experiments to assess how a rodent responded to perceptions of habitat risk in the two different habitats. This could also be thought of as a “perception experiment” (experiment Type I.1 in Jenerette & Shen, 2012), but one that examines an animal’s perception of the landscape pattern. Because GUDs are relative easy to deploy, and the landscape contained many woody patches, the researchers were able to replicate across 50 wooded patches, with 8 GUDs per patch along a gradient from the grassland habitat through the edge and into the wooded patch (Abu Baker & Brown, 2010). Grasslands and agricultural systems have also been shown to be amenable to tracer experiments, for example by using dye tracers to assess water flow (Wang et al., 2019) or by applying telemetry devices to small organisms, such as salamanders (Cosentino et al., 2011). As with the forested systems, controls are relatively easy to obtain in these grassland experiments, simply by taking measurements in areas of the grassland that the researchers did not expose to a manipulation. In the IMGRE site, the study area is large enough to accommodate controls for the manipulation and also facilitate additional observational studies (Chen et al. 2015a, b) that complement the manipulative

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experiments. Randomization requires similar considerations of underlying gradients as in forests. Replication appears to be similar to or higher than found in forest experiments; the IMGRE project has 8 replicate blocks (Wu et al., 2015), which is comparable to the replication level in many of the large-scale forest experiments. In contrast, the grazing study by Kay et al. (2017) is replicated across 29 farms divided between 4 blocks and Abu Baker and Brown (2010) were able to replicate their GUD experiment across 50 sites.

6.3.3  Aquatic Experiments As all good landscape ecologists know, landscape ecology is not limited to terrestrial systems (Wiens, 2002). Aquatic systems, particularly lakes and ponds, are amenable to large-scale experiments because they represent contained systems. The most famous example of an aquatic experimental system is probably the Hubbard Brook LTER site. Although this is a large-extent study, it did not have an explicit landscape ecology focus. However, researchers have carried out different experiments at Hubbard Brook that have a spatial dimension, including comparing water characteristics in an experimentally cleared watershed to a control (Burton & Likens, 1973) or tracer experiments that compare addition of chemicals in one watershed to a control (e.g., Likens et al., 2017). Similar experiments with nutrient additions have famously demonstrated eutrophication at a large extent at the Experimental Lakes Area (ELA) in northwestern Ontario (Schindler, 1998). While most of these have a clear manipulation and control, they often lack replication, and only treat a single watershed or lake with the experimental application. This may be due in part to cost and logistics, or to the impossibility of finding multiple watersheds or lakes that are nearly identical. Nonetheless, despite the lack of replication, they are clearly experimental, and the evidence is so compelling about the impact that the lack of replication may not be a major concern. Thinking of lakes or watersheds as ‘patches’ influenced by the surrounding matrix may open up possibilities for using waterbodies for different kinds of experiments in landscape ecology to address questions about gradients, connectivity, and matrix properties.

6.4  What Have We Learned from Large-Scale Manipulations? Large-scale manipulative experiments probably best match what many people imagine when they think about a “landscape experiment”. Ongoing large-scale experiments have helped us to identify landscape-scale variation in processes, such as how species adapt to particular locations, or how landscape characteristics such as cover type or ambient noise affects animal movement. They have also helped us

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to understand how landscape structure and pattern affects spatial processes, including how fragmentation and patch size/shape affect species’ persistence and movement as well as things like nutrient flow. The spatial extent of such experiments introduces logistical constraints, and the longevity of many of these studies is both impressive and highly valuable. Landscape ecologists are not the only ones to explore large-scale manipulations. Fayle et al. (2015) review a suite of over 20 whole-ecosystem experimental manipulations in tropical forests. Although not all of these experiments address explicitly landscape ecology questions, these sites and systems could be useful places to explore for landscape ecologists seeking to do large-scale experiments. While the design of many large-scale manipulative experiments are elegant, and demonstrate careful thought to implementation of experimental controls and random sampling, it can be difficult to have extensive treatment replication. Despite this, these studies have given us many valuable insights on the impact of human activities (e.g., clearcutting, nutrient inputs from agricultural runoff) on natural systems that would not be possible without such experiments. Some might criticize these large-scale experiments as being limited to inferences about their particular location as they are very much “place based”. I do not think this is necessarily a concern; multiple examples of similar types of experiments across different biomes (as we saw in the forested landscapes examples) can lead to broader inferences over time. We have learned much from large-scale experiments, particularly about how organisms respond to landscape change over time. At the end of the next chapter, I will provide a summary of what we have learned from analyses across both large-­ scale experimental manipulations (the subject of this chapter) and experimental model landscapes (the subject of the next chapter), since both share similarities in terms of research questions and approaches. There are important ethical considerations when manipulating large landscapes. For example, the aquatic manipulations at the ELA may adversely affect the biota of the waterbody. The SAFE project website explicitly explains that the project is not causing deforestation but is harnessing planned oil palm conversion for experimental purposes. Researchers need to balance the ethical trade-off between experimental habitat destruction and insights that might benefit conservation science. This is not easy—thus collaborating with planned anthropogenic activities, such as is the case at SAFE and Calling Lake—helps alleviate these ethical issues to an extent. In tandem with this is the need for effective partners. The Calling Lake project required co-operation from the forest company to modify their harvest plan to match the experimental design. The BDFFP and SAFE projects are in the global south, where working with local community partners is critical to successful collaboration and to avoid colonial (de Vos, 2020) or parachute (Stefanoudis et al., 2021) science. Because of their logistical challenges, large-scale manipulative experiments require long-term work to yield results. Thus, they are not advisable for early career researchers with limited funding and time to initiate. They operate best when run by a research centre or university or by a consortium of researchers. Consequently, a graduate student or early-career researcher given the opportunity to work at one of these existing large-scale experiments would have a tremendous opportunity. The

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extent and longevity of many of these sites means there is already a wealth of knowledge and data from which to begin. Projects like the BDFFP and SAFE have served as attractors for researchers from around the world, and their websites provide clear guidelines and information for anyone considering working in the area (see Resources section for details). New researchers keen to embark on this type of experiment, especially for graduate research, would be wise to work on one of the long-term projects and focus on an organism or process with a relatively quick response time, such that one can gain meaningful data within the timeframe of a graduate degree. Meta-analyses of data from the various large-scale experiments can yield broader insights into ecological concepts (see Haddad et  al., 2015 for an example). Distributed experiments across sites would be logistically challenging but not impossible, especially in our increasingly networked world. The G-TREE (Global Treeline Range Expansion Experiment) is an example of a globally distributed biogeography experiment whereby researchers working on treeline research have an agreed-upon sampling protocol and data sharing standards that enables both fine-­ scale and broad-scale analysis (Brown et al., 2013). Researchers in landscape ecology could create similar agreed-upon protocols for landscape ecology questions. Such a strategy need not be expensive; the G-TREE was developed by the project lead as a “side project” during her postdoc, harnessed freely-available online tools to communicate, and relies on the individual project leads to fund their field work. Synthesis across projects happens via the internet and through sponsored in-person workshops. While the project is larger in scope than a single post-doc position, the G-TREE initiative spun into profitable early-career collaborations for many of the team members. Large-scale experiments also work well when complemented by other types of experiments, such as some of the ones discussed in the next few chapters. For example, we can use data from the real world to parameterize spatial models (in silico experiments, Chap. 10), or we can construct model mesocosms (Chap. 8) that capture aspects of the real world at larger scales, but under more highly controlled conditions. By integrating findings between experimental types, and within similar experiments from around the world, landscape ecologists can really begin to harness fully the power of experiments to advance our field.

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Chapter 7

Experimental Model Landscapes

7.1  What Are Experimental Model Landscapes? For the purposes of this book, experimental model landscapes are defined as being not as large in extent as the large-scale experiments described in the previous chapter, but larger than meso- or microcosm experiments (which are discussed in the next two chapters). They are generally only a few hectares, and sometimes only a few hundred square metres in area. In addition, most of them are in mowed fields or modified agricultural systems that have less complex land cover than the experiments described in Chap. 6. The smaller spatial extent and more human-modified landscape means that the researcher has more control over the experiment and can more easily isolate whether the factor of interest is affecting the experimental outcome. If you were to take a bird’s eye view of some of the experimental model landscapes described in this chapter, they would look different from many of the large-­ scale manipulations discussed in the previous chapter for a number of reasons. In addition to covering a smaller extent, in these experimental model landscapes, most, if not all, of the study area is manipulated in some way. This is in contrast to the patches of manipulations embedded in a natural matrix that are more typical of the large-scale manipulative experiments. The model landscape would more closely resemble an idealized experimental design such as a scientist might sketch out on their whiteboard. Instead of needing to put experimental treatments where they “fit” in the natural landscape, and replicating them in places where the landscape is as similar as possible, in an experimental model landscape, the researcher generally can more carefully control the size, shape and placement of the treatments. Figure 7.1 is a photo of the Bowling Green Fragmentation Experimental Model Landscape System; a 4-ha experiment in Ohio, which has become a “poster child” for experiments in landscape ecology. Similar projects (Kansas Fragmentation Experiment (Fig. 7.2), the Evenstad experiments, Jena Experiment) have – on the face of it  – a similar experimental design consisting of patches created through © Springer Nature Switzerland AG 2022 Y. F. Wiersma, Experimental Landscape Ecology, Landscape Series 29, https://doi.org/10.1007/978-3-030-95189-4_7

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Fig. 7.1  Aerial image of the Bowling Green Fragmentation Model Landscape System near Bowling Green State University, Ohio, USA. (Used with permission from Oxford University Press and Kim With)

mowing or weeding, and aerial images of these types of studies show a design in which the researchers have laid experimental blocks very evenly and precisely. Careful examination of the pattern(s) of the experimental blocks will reveal a random or stratified random placement of the treatments, as well as close-to-even replication of each treatment level. This kind of precision and care in the design is not possible to the same degree in a large-scale manipulation embedded in a natural system. Despite similarities in appearance, the underlying framework for landscape construction, as well as the theoretical basis for the different manipulations, varies between experimental model landscapes. I will discuss some of these key differences in the case examples below. Nonetheless, experimental model landscapes have advantages for research. The limited extent of the study area, and the fact that many are in agricultural fields, means that their land cover is generally more homogenous than the sites discussed in the previous chapter. Thus, many of these experimental model landscapes can also encompass a wider number of treatments (and levels per treatment) than large-scale landscape manipulations. In addition, these types of studies can allow an experimental design that can randomize the placement of the various treatment plots more easily. Replication can also be a little more extensive in these model experiments compared to the experiments described in the previous chapter. For example, in the Jena experiment in Germany, Roscher et al. (2004) were able to have 90 plots (20 × 20 m each) with between 8 and 72 replicates per treatment, and 5 treatment levels. The placement of the plots followed a randomized block design, with blocks delineated based on soil type (Roscher et al., 2004). At Bowling Green, With and Pavuk (2011) had two treatments, habitat

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Plant quadrats Small mammal trap stations Woody canopy Patch/study area boundaries Second growth forest Brome field

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Fig. 7.2  Diagram of the Kansas University Fragmentation Experiment. (Original figure from Schweiger et al. (2000) and used here with permission of Wiley Ltd.)

amount and degree of fragmentation, with six levels of habitat amount (10, 20, 40, 50, 60 and 80%) and two levels of fragmentation (clumped and fragmented). Their study space allowed them to have three replicates of each treatment combination. Experiments at Evenstad had between four (Ims et al., 1993) and seven (Andreassen & Ims, 1998) replicates. Unlike large-scale studies embedded in a less-intensively managed landscape, these studies do not always have a natural “control” area for comparison. Rather, researchers often manipulate treatment levels in a careful design to control for confounding effects. For example, in the Bowling Green experiment, With and Pavuk (2011) wished to assess the effect of fragmentation on arthropod richness. Because it can be difficult to tease apart the effect of habitat fragmentation vs. habitat loss (Fahrig, 2003), With and Pavuk (2011) created plots of clover and non-clover habitat, with identical amounts of habitat but different levels of fragmentation (clumped and fragmented). In the Jena experiment, which focused on the effects of within-plot diversity, plots that had the full complement of natural species composition as well as bare-ground plots, which together functioned as the experimental controls (Roscher et al., 2004). Experimental model landscapes can address some of the same types of questions as large-scale manipulations (Table 7.1)—especially those that identify how patch shape, connectivity and fragmentation affect landscape processes (Type III.8–10 in Jenerette & Shen, 2012). The smaller scale of these model systems makes it more

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Table 7.1  Taxonomy of types of landscape experiments (sensu Jenerette & Shen, 2012), with bold font indicating the type of experiment for which experimental model landscapes are especially-­ well suited, and italic font for those types which it may be possible to harness these, but for which other experimental approaches may be better suited. References describing examples of experimental model landscapes of each type are given; these are not exhaustive Group I. Identification of landscape structure II. Identification of process variation within landscapes

III. Identification of process sensitivity to landscape structure

Type of experiment 1. Perception experiment 2. Tracer experiments 3. In situ experiments distributed throughout a landscape 4. Ex situ experiments using samples collected throughout a landscape 5. Translocation experiments 6. Transport manipulations 7. Manipulation of internal patch characteristics 8. Manipulation of patch shape 9. Manipulation of patch connectivity 10. Fragmentation experiments

IV. Identification of landscape pattern formation factors

11. Manipulation of landscape scale 12. Construction of entire landscapes 13. Manipulative disturbances 14. Vector manipulations

Example

Roscher et al. (2004) and Weisser et al. (2017) Collinge (1998) and Collinge (2000) Collinge (2000) Collinge (1998), Golden and Crist (1999) and With and Pavuk (2011)

Stokstad (2012) Vogel et al. (2019)

difficult to conduct experiments that manipulate internal patch characteristics than in large-scale manipulations, and some of the experimental types we saw in the previous chapter, such as tracer experiments, translocation experiments, transport manipulations, and disturbance studies are possible, but perhaps less generalizable in these systems. However, their tractable size makes it possible to create entire landscapes scaled for the organisms of interest, thereby allowing for experiments that fit Type III.12 in Jenerette and Shen (2012)—an experiment type not possible in the systems described in the previous chapter. Many of these created landscapes simultaneously address experimental questions around fragmentation or patch patterns (e.g., McIntyre & Wiens, 1999; With et al., 1999; With & Pavuk, 2011).

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7.2  A  dvantages and Disadvantages of Experimental Model Landscapes Experimental model landscapes share some of the advantages of realism seen with the large-scale manipulative experiments discussed in the previous chapter. Since they tend to be located in more simplified agricultural systems than the larger manipulations found in natural forests or grasslands, they can have the added advantage of it being easier to avoid confounding effects of unexpected natural processes. They can still be subject to unexpected natural disturbances, such as a fire, windstorm, or flood, but because their environments are under more anthropogenic control within human-dominated landscapes, experimental model landscapes generally have more immunity to disturbances. Experimental model landscapes can be logistically challenging to set up and maintain. To avoid invasion into the experiment by plants from outside the study area, frequent weeding (With & Pavuk, 2011) or mowing (Holt et al., 1995) can be necessary along with tilling of the surrounding matrix to keep patches isolated from each other (With et  al., 2002). At the Jena field site, pre-treatment of the site to reduce weeds involved harrowing (five treatments over multiple months) and a treatment with herbicide. The sampling work can also be tedious and time-­ consuming, even if the focal organisms are small (e.g., insects) or stationary (e.g., plants). For example, at the Bowling Green site, With et al. (2002) reported that it could take up to 4 h to survey the 16 × 16 m plots with 80% clover cover for insect species. This does not include the time required to identify species—With (pers. comm.) reported that in one survey of microarthropods, they collected over 24,000 individuals that ended up belong to 270 morphospecies, which took years to classify. Researchers who want to carry out an experimental model landscape such as the ones described below require access to a reasonably sized area, over which they can control the configuration of cover. The high level of labour required to maintain these sites means they should ideally be near research campuses. At the same time, they should not be accessible to the public, to avoid interference with the experiments. At Bowling Green for example, it was necessary to construct a chain link fence around the entire 4-ha site (With pers. comm.), as the site was along a gravel road near the campus. The fact that there are not many of these large-scale experimental models in the landscape ecology literature speaks to the challenges of establishing them.

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7.3  Case Examples 7.3.1  Bowling Green Experimental Model Landscape System Landscape ecologist Kimberly With and entomologist Daniel Pavuk at Bowling Green State University in Ohio, USA, initiated this system in 1997. The beauty of this system is that the experimental plots of clover/bare ground (Fig. 7.1) are real-­ world representations of fractal neutral landscape patterns (With, 1997), which were generated in silico using the software RULE (Gardner, 1999). The advantage of fractal models is that the researchers could tease apart the effect of habitat amount and fragmentation, by independently varying the amount of habitat (p) and the degree of spatial contagion or fragmentation (measured using the Hurst dimension (H)). Thus, their experimental setup illustrates the value of combining different experimental approaches to address a research question (Jenerette & Shen, 2012). In the field, the researchers divided each 16 × 16 m plot into 1 × 1 m “cells”, each of which matched a pixel in the in silico neutral landscapes created in RULE. The experimental design has two treatments, habitat amount and habitat fragmentation. Habitat amount is configured across six levels, ranging from 10% clover cover to 80% clover cover and habitat fragmentation is set at two levels; H = 1.0 (clumped) and H = 0.0 (fragmented). Each treatment/level is replicated three times, yielding 36 experimental plots within 4 ha (With & Pavuk, 2011, 2019). This system has yielded numerous publications; one of the studies examined how fragmentation pattern affected arthropod diversity (With & Pavuk, 2011). In this experiment, the researchers surveyed the natural diversity of arthropods within each of the 36 patches to assess how habitat amount and degree of fragmentation affected diversity patterns at both the landscape (With & Pavuk, 2011) and patch (With, 2016) levels. They found that arthropod species richness correlated to overall habitat amount rather than the degree of fragmentation. To see if smaller organisms responded differently to the experimental fragmentation, they also sampled for microarthropods in the same system (With & Pavuk, 2012), and looked at their response to landscape configuration and associated edge effects. In the year following the initial fragmentation experiment  set-up and arthropod surveys, With and Pavuk (2019) carried out another study examining how fragmentation affected parasitism by surveying the clover patches for aphids and their parasites, with the goal of understanding how landscape pattern might affect biocontrol of insect pests (With et  al., 2002). The fragmentation experiments at Bowling Green have also yielded important insights about the impacts of habitat fragmentation (With, 2016) that might be scaled to larger-extent landscapes.

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7.3.2  University of Kansas Habitat Fragmentation Facility The University of Kansas Field station is over 1375 ha in size and contains a number of different research facilities. The one germane to this chapter is the 12-ha Habitat Fragmentation Facility, which has been in operation since 1984. The experimental design consists of a 12-ha field that had previously been farmed, and then left fallow for 9 years prior to the experimental mowing. The experiment aimed to assess how patch size and isolation affected plant succession patterns (Holt et al., 1995). To that end, the experimental patches were mowed to one of three different sizes (32 m2, 288 m2 and 0.5 ha). The experimenters designed the experimental units as either one 0.5 ha patch, or clusters of 6 of the medium patches or 15 of the smallest patches; the clusters were spaced in such a way that the perimeter of the experimental unit was the same across all three size classes (Fig. 7.2). Thus, the inter-patch distance was greatest for the smallest (32 m2) patches. The researchers used a stratified random array to place the patch units, and replicated each size class six times for the largest and smallest sized patches and three times for the medium patches (Holt et  al., 1995). Research papers from this site have examined how the patch size affected vegetation dynamics (Holt et al., 1995; Yao et al., 1999; Cook et al., 2002), as well as how the fragmentation affected small mammal movement (Diffendorfer et al., 1995; Schweiger et al., 2000; Cook et al., 2004) and insect successional patterns (Martinko et al., 2006). The Kansas Habitat Fragmentation experiment is the longest-running example of an Experimental Model Landscape.

7.3.3  Miami University Old-Field Experiment Miami University, in Oxford, Ohio, has dedicated part of its 69-ha field station for experimental models using mowed field plots, in different configurations over the years, led by ecologist Thomas Crist. In 1995, a 1-ha goldenrod field was mowed to create 16 plots (13 × 13 m each) that were further subdivided into 9 fragments of different sizes (1 m2, 4 m2, 9 m2, and contiguous) to control for patch number and shape but change patch size and isolation (Golden & Crist, 1999, 2000). The researchers used a Latin square design instead of random placement so that they could block the treatments by row/column and avoid having the same treatment more than once in each row, column or corner of the field. This helped minimize any effects due to variation in growing conditions across the field. Golden and Crist (1999) used this experimental set-up to test how habitat fragmentation affects insect communities at both the guild- and species- level, and to assess how beetles and ants were influenced by patch area vs. edge habitat (Golden & Crist, 2000). Crist and Ahern (1999) used it to assess beetle abundance and distribution using mark-­ recapture techniques. In a nearby old field, Summerville and Crist (2001) created a second mowing experiment in 1999. This design was a little larger than the previous one, and

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consisted of 25 plots, each 15 m × 15 m in size. There were five fragmentation treatments, each replicated five times, and as with the earlier experiment, laid out in a Latin square design. The focus of this project was fragmentation in combination with patch quality (measured as the amount of flowering plant cover), and its effect on butterflies. The hypothesis here was that moderately fragmented patches might have the highest species richness and abundance, and thus the better quality for butterflies (Summerville & Crist, 2001). Other researchers leveraged this design and data to assess questions about species nestedness across scales (Summerville et al., 2002) and the spatial variation in both plant and insect communities as a result of habitat loss and edge creation (Crist et al., 2006). An even larger experiment in 2004 established 36 plots (14 m × 14 m in size) and maintained habitat area independent of fragmentation while also examining matrix effects (Diekötter et al., 2007). Patches of clover varied in habitat amount at two levels (4 m2 or 16 m2); in matrix type (orchard and bare ground); and had two levels of fragmentation (single continuous plot or four separated subplots). The experimental design replicated each combination of habitat area/fragmentation/matrix type four times. Diekötter et al. (2007) used this experiment to survey for insects to see how they responded to the experimental manipulation, while Haynes and Crist (2009) examined how these factors affected insect herbivory and Haynes et  al. (2007) tested for the response of a species  of grasshopper using mark-recapture techniques. All of these experiments at Miami University’s field station share similar designs and with the Kansas University and Bowling Green experiments in that they use mowing, weeding and herbicides to rigorously maintain patches of different cover types in an agricultural setting and measure the response of insects or small mammals of one type or another. Each adds something slightly different. The fragmentation pattern at Bowling Green mimics neutral landscapes created in a computer model, while the fragmentation in the Kansas Fragmentation Experiment and in the first set of experiments at Miami University were generated by systematically shrinking the size of the subplots. In the Miami experiment, sub-plot shrinkage maintained the patch pattern of 3 × 3 subplots, while at Kansas the manipulation preserved the perimeter of the experimental unit across treatments. The fragmentation patterns in the second Miami University experiment (Summerville & Crist, 2001) resemble the neutral landscapes created at Bowling Green. However, they differ in that they were not created using in silico neutral models but rather were created by subdividing the 15 m × 15 m plot into 25 subplots (3 m × 3 m each) and then randomly selecting subplots for mowing, to achieve the desired remaining habitat amount (20, 40, 60 or 80%). This is a critical difference in the manipulation; the Bowling Green experiment creates fragmented landscapes using what With (2016) referred to as a “top down” approach by manipulating habitat amount and spatial contagion, while the Kansas University and Miami University fragmented landscapes are created using a “bottom up” (sensu With, 2016) process of changing the size and spacing of patches.

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7.3.4  Collinge Experiments Collinge (2000) carried out a fragmentation experiment in a ~3 ha native mixed-­ grass prairie in Colorado, USA and examined insect responses. Treatments included patch size (three levels) and connectivity (control, corridor and isolated) arranged in a split-plot design, with six replicates. What is unique about this design compared to the ones discussed in this chapter to this point is that the controls were sample plots embedded in an intact matrix, much as we saw in some of the large-scale manipulative experiments in the previous chapter (e.g., the Calling Lake Fragmentation Experiment, Schmiegelow et  al., 1997). In a parallel study at the same site, Collinge (1998) mimicked four sequences of land conversion (shrinkage, bisection, fragmentation and perforation) in 10 m × 10 m plots, each replicated five times, with a four-day interval between each stage of mowing to realize the final design. As with all the model systems discussed in this chapter, this study used insect diversity as the response variable, and sampled in between each mowing event, as well as in control (un-mowed plots) and both immediately after and 5 weeks following the final mowing (Collinge, 1998; Collinge & Forman, 1998). Because the study site was on property owned by the City of Boulder, not part of a university research centre, it does not appear that research continued long-term on these experimental plots as they have at some of the other sites, such as the University of Kansas site or the Jena experiment. Nonetheless, a few years later, as a professor at University of California, Davis, Collinge and her graduate student Todd Palmer, designed another landscape model, this time in a smaller area (30 m × 80 m). This design manipulated plot shape (squares vs. rectangles) while maintaining area, and boundary contrast (created by planting different heights of grass in the centre and the edges of the plots; Collinge & Palmer, 2002).

7.3.5  Evenstad Experiments Ecologist Rolf Ims and colleagues have conducted a suite of experiments using rock voles (Microtus oeconomus) as a model system. Their focus has been on demographic and behavioural responses of voles to different patterns of habitat fragmentation. Different experiments have manipulated patch size (Ims et al., 1993), and isolation (Ims & Andreassen, 2005) alone as well as combined factorial experiments that addressed patch size and isolation (Andreassen & Ims, 1998; Johannesen et al., 2000) or patch size and connectivity (Andreassen et al., 1998; Bjornstad et al. 2009). Patch size was scaled to be such that the smallest patches (225 m2) were sufficiently large to contain a vole home range (Johannesen et al., 2000) and maximum inter-­ patch distance (15 m) was scaled such that movement between patches was possible, but not common. These experiments illustrate that it is possible to create landscapes that are small enough to manipulate experimentally but that match the scale of the focal organism. Indeed, Ims et al. (1993) were initially motivated to use

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rock voles as a model system to assess the impacts of fragmentation on a larger, more wide-ranging species of conservation importance, the capercallie grouse (Tetraao urogallus). Because experimental manipulation of capercallie habitat was not feasible, they used observational studies of how their space use responded to fragmentation cause by forest harvest, and compared this to the vole response in a highly manipulated experiment.

7.3.6  Jena Experiment The Jena experiment, just southwest of Leipzig, Germany, involves a consortium of researchers from different universities and research centers. The project has been ongoing since 2002. Although the focus is on research in ecosystem functioning, and not landscape ecology processes, the experimental manipulations represent a type of landscape experiment. Here, the manipulation of internal patch characteristics (in this case plant species richness within replicate plots) is an example of Jenerette and Shen’s (2012) Type III.7 experiment. The primary goal of the Jena experiment is to assess how biodiversity affects ecological processes, such as nutrient cycles, as well as biodiversity patterns. It is similar to the Cedar Creek experiments that have been running much longer (Tilman, 2009). Although the research at Jena and Cedar Creek are not explicitly testing hypotheses based on landscape ecology concepts, their experimental design has to take spatial pattern into consideration (see detailed layout of the Jena experiment in Weisser et al., 2017), and the experiments themselves manipulate internal patch characteristics (Type III.7  in Jenerette & Shen, 2012). With some creativity, landscape ecologists could use sites like Jena and Cedar Creek to address more spatially explicit questions. At Jena, the researchers selected subsets of grassland plant species from a pool of 60 species, and planted these in 82 plots (20 m × 20 m each) in treatments of 1 (monoculture) to 16 species, with control plots of bare ground and the full suite of 60 species. The researchers configured the species subsets to assess plant diversity in terms of both species, and plant functional type, and laid the plots out following a stratified random design along soil gradients (Roscher et  al., 2004; Weisser et al., 2017). Researchers have used the Jena site to assess how plant species diversity affects arthropod diversity (Hertzog et  al., 2016) as well as the effects of disturbance (experimental drought and fertilization) on community diversity and stability (Vogel et al., 2019). The Jena site has some differently sized plots (Vogel et al., 2019); these serve a different purpose than to test for questions about patch size effects. However, one could imagine a design such as this one being harnessed to test questions about patch/landscape patterns such as the effects of patch shape and configuration on disturbance drivers, and whether and how patch diversity is affected by patch patterns.

7.4  What Have We Learned from Large-Scale Studies?

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7.4  What Have We Learned from Large-Scale Studies? Experimental model landscapes can be very elegant, and offer valuable insights into effects of patch and landscape characteristics on biodiversity. Experiments in these systems have helped to differentiate between the effects of patch area and isolation (for example, as manipulated at Evanstad; Ims et al., 1993; Johannesen et al., 2000; Bjornstad et  al., 2009) versus habitat amount and fragmentation “per se” (sensu Fahrig, 2003), which is the focus of the Bowling Green experiment (With & Pavuk, 2011). The papers cited in this chapter use different focal organisms (insects, plants, small mammals) which helps to demonstrate how fragmentation can have differing effects—it can be negative for some species, but positive for others. Comparisons between findings from experimental model landscapes and from large-scale manipulative experiments (Chap. 6) which frequently focus on similar questions can be useful to gain broader insights from these kinds of experiments. For example, Collins et  al. (2017) synthesized findings from the Kansas Fragmentation experiment (discussed in this chapter) along with three of the experiments discussed in the preceding chapter: BDFFP, Wog Wog, and the Savannah River Site. They specifically examined how fragmentation affected plant community composition in these experiments and asked whether there were similarities between the experiments. They noted that the process for experimentally creating fragments differed—in Wog Wog and the BDFFP, fragments were created by clearing intact forest around them, and thus plant communities were affected by isolation and fragment size effects; while at Kansas and Savanah River, the fragments were clearings that were left to allow communities to develop through succession. At the latter two sites, Collins et al. (2017) did not observe divergence in community composition, while they did at the former two. They caution however, that any general interpretations about community composition responses to fragmentation are limited when only comparing four studies (Collins et al., 2017). In a broader survey, Debinski and Holt (2000) surveyed twenty fragmentation experiments around the world, including many of those mentioned in this chapter and the preceding one. Their findings corroborate much of what I have summarized about large-scale manipulative experiments and experimental model landscapes. The research using these systems tends to focus on issues around species richness, connectivity/isolation, species behaviour, demography and genetics. Across sites, they found support for a given hypothesis in some, but not all, experiments (Debinski & Holt, 2000). How species respond to fragmentation is often an organism-specific response or is subject to the design aspects of the specific experiment—such as whether the fragmentation is created though a top-down or bottom-up process (sensu With, 2016), or whether the experimental unit is focused on the patch or the landscape level. Haddad et  al. (2015) carried out a meta-analysis across several long-running fragmentation experiments, including four discussed in the previous chapter (SAFE, BDFPP, Wog Wog and Savannah River) the Kansas Fragmentation experiment (discussed in this chapter) as well as a mesocosm (Chap. 8) and microcosm (Chap. 9)

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experiment. They evaluated how reduction in patch area, increase in patch isolation and increase in patch edge affected species-, ecosystem- and community-level responses and found strong and consistent responses across taxa and systems (Haddad et al., 2015). However, their focus on patch-level responses, rather than landscape-level ones means there is room for more research in this area. While this, and other work (Haddad et  al., 2017), suggest a lack of support for the habitat amount hypothesis (Fahrig, 2013), others have found an opposite pattern when synthesizing data across projects (Watling et al., 2020). Large-scale experiments are an ideal method for addressing this hypothesis, though as shown in these two chapters, large-scale experiments are not limited to testing hypotheses about fragmentation. Finally, in a survey of conservation experts, Resasco et al. (2017) examined the links between theoretical developments of island biogeography, metapopulation theory and metacommunity dynamics and experiments on fragmentation to conservation applications. They concluded that what the academic community studies does not always match the needs of the conservation practitioners. Their review encompassed several of the large-scale manipulations described in Chap. 6, as well as a microcosm and mesocosm experiment, which I discuss in the next two chapters. Increased complementarity between the two types of large-extent experiments, as well as between these models and other experiments (e.g., in silico ones as used in the Bowling Green design) will serve to help our discipline realize broader, more universal insights, while perhaps also assisting with applied conservation challenges.

References Andreassen, H., & Ims, R. (1998). The effects of experimental habitat destruction and patch isolation on space use and fitness parameters in female root vole Microtus oeconomus. Journal of Animal Ecology, 67, 941–952. Andreassen, H., Hertzberg, K., & Ims, R. (1998). Space-use responses to habitat fragmentation and connectivity in the root vole Microtus oeconomous. Ecology, 79, 1223–1235. Bjornstad, O., Andreassen, H., & Ims, R. (2009). Effects of habitat patchiness and connectivity on the spatial ecology of the root vole Microtus oeconomus. Journal of Animal Ecology, 67, 127–140. Collinge, S.  K. (2000). Effects of grassland fragmentation on insect species loss, colonization, and movement patterns. Ecology, 81, 2211–2226. https://doi.org/10.1890/0012-­9658(2000)08 1[2211:EOGFOI]2.0.CO;2 Collinge, S. K. (1998). Spatial arrangement of habitat patches and corridors: Clues from ecological field experiments. Landscape and Urban Planning, 42, 157–168. https://doi.org/10.1016/ S0169-­2046(98)00085-­1 Collinge, S.  K., & Forman, R.  T. T. (1998). A conceptual model of land conversion processes: Predictions and evidence from a microlandscape experiment with grassland insects. Oikos, 82, 66–84. Collinge, S. K., & Palmer, T. M. (2002). The influences of patch shape and boundary contrast on insect response to fragmentation in California grasslands. Landscape Ecology, 17, 647–656. https://doi.org/10.1023/A:1021536302195 Collins, C., Banks-Leite, C., Brudvig, L., et al. (2017). Fragmentation affects plant community composition over time. Ecography, 40, 119–130.

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Cook, W. M., Lane, K. T., Foster, B. L., et al. (2002). Island theory, matrix effects and species richness patterns in habitat fragments. Ecology Letters, 5, 619–623. Cook, W. M., Anderson, R., & Schweiger, E. (2004). Is the matrix really inhospitable? Vole runway distribution in an experimentally fragmented landscape. Oikos, 104, 5–14. Crist, T. O., & Ahern, R. G. (1999). Effects of habitat patch size and temperature on the distribution and abundance of ground beetles (Coleoptera: Carabidae) in an old field. Environmental Entomology, 28, 681–689. https://doi.org/10.1093/ee/28.4.681 Crist, T. O., Pradhan-Devare, S. V., & Summerville, K. S. (2006). Spatial variation in insect community and species responses to habitat loss and plant community composition. Oecologia, 147, 510–521. https://doi.org/10.1007/s00442-­005-­0275-­1 Debinski, D. M., & Holt, R. D. (2000). A survey and overview of habitat fragmentation experiments. Conservation Biology, 14, 342–355. Diekötter, T., Haynes, K. J., Mazeffa, D., & Crist, T. O. (2007). Direct and indirect effects of habitat area and matrix composition on species interactions among flower-visiting insects. Oikos, 116, 1588–1598. https://doi.org/10.1111/j.2007.0030-­1299.15963.x Diffendorfer, J. E., Gaines, M. S., & Holt, R. D. (1995). Habitat fragmentation and movements of three small mammals (Sigmodon, Microtus, and Peromyscus). Ecology, 76, 827–839. Fahrig, L. (2003). Effects of habitat fragmentation on biodiversity. Annual Review of Ecology, Evolution, and Systematics, 34, 487–515. Fahrig, L. (2013). Rethinking patch size and isolation effects: The habitat amount hypothesis. Journal of Biogeography, 40, 1649–1663. https://doi.org/10.1111/jbi.12130 Gardner, R.  H. (1999). RULE: Map generation and spatial analysis program. In J.  Klopatek & R. H. Gardner (Eds.), Landscape ecological analysis: Issues and applications (pp. 280–303). Springer. Golden, D. M., & Crist, T. O. (2000). Experimental effects of habitat fragmentation on rove beetles and ants: Patch area or edge? Oikos, 90, 525–538. https://doi.org/10.1034/j.1600-­0706.2000. 900311.x Golden, D. M., & Crist, T. O. (1999). Experimental effects of habitat fragmentation on old-field canopy insects: Community, guild and species responses. Oecologia, 118, 371–380. https://doi. org/10.1007/s004420050738 Haddad, N. M., Brudvig, L. A., Clobert, J., et al. (2015). Habitat fragmentation and its lasting impact on Earth’s ecosystems. Science Advances, 1, e150005. Haddad, N. M., Gonzalez, A., Brudvig, L. A., et al. (2017). Experimental evidence does not support the habitat amount hypohthesis. Ecography, 40, 48–55. Haynes, K. J., & Crist, T. O. (2009). Insect herbivory in an experimental agroecosystem: The relative importance of habitat area, fragmentation, and the matrix. Oikos, 118, 1477–1486. https:// doi.org/10.1111/j.1600-­0706.2009.17720.x Haynes, K. J., Diekötter, T., & Crist, T. O. (2007). Resource complementation and the response of an insect herbivore to habitat area and fragmentation. Oecologia, 153, 511–520. https://doi. org/10.1007/s00442-­007-­0749-­4 Hertzog, L. R., Meyer, S. T., Weisser, W. W., & Ebeling, A. (2016). Experimental manipulation of grassland plant diversity induces complex shifts in aboveground arthropod diversity. PLoS One, 11, 1–16. https://doi.org/10.1371/journal.pone.0148768 Holt, R. D., Robinson, G. R., & Gaines, M. S. (1995). Vegetation dynamics in an experimentally fragmented landscape. Ecology, 76, 1610–1624. Ims, R. A., & Andreassen, H. P. (2005). Density-dependent dispersal and spatial population dynamics. Proceedings of the Royal Society B, 272, 913–918. Ims, R. A., Rolstad, J., & Wegge, P. (1993). Predicting space use responses to habitat fragmentation: can voles Microtus oeconomus serve as an experimental model system (EMS) for Capercaillie grouse Tetrao urogallus in boreal forest? Biological Conservation, 63, 261–268. Jenerette, G.  D., & Shen, W. (2012). Experimental landscape ecology. Landscape Ecology, 27, 1237–1248. https://doi.org/10.1007/s10980-­012-­9797-­1 Johannesen, E., Andreassen, H. P., & Ims, R. A. (2000). Spatial explicit demongraphy: the effect habitat patch isolation have on vole matrilines. Ecology Letters, 3, 48–57.

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Martinko, E. A., Hagen, R. H., & Griffith, J. A. (2006). Successional change in the insect community of a fragmented landscape. Landscape Ecology, 21, 711–721. McIntyre, N.  E., & Wiens, J.  A. (1999). Interactions between landscape structure and animal behavior: The roles of heterogeneously distributed resources and food deprivation on movement patterns. Landscape Ecology, 14, 437–447. https://doi.org/10.1023/A:1008074407036 Resasco, J., Bruna, E. M., Haddad, N. M., et al. (2017). The contribution of theory and experiments to conservation in fragmented landscapes. Ecography, 40, 109–118. Roscher, C., Schumacher, J., Baade, J., et al. (2004). The role of biodiversity for element cycling and trophic interactions: An experimental approach in a grassland community. Basic and Applied Ecology, 5, 107–121. Schmiegelow, F. K. A., Machtans, C. S., & Hannnon, S. J. (1997). Are boreal birds resilient to forest fragmentation? An experimental study of short-term community responses. Ecology, 78, 1914–1932. https://doi.org/10.1890/0012-­9658(1997)078[1914:ABBRTF]2.0.CO;2 Schweiger, E. W., Diffendorfer, J. E., Holt, R. D., Pierotti, R., & Gaines, M. S. (2000). The interaction of habitat fragmentation, plant and small mammal succession in an old field. Ecological Monographs, 70, 383–400. Stokstad, E. (2012). Experimental landscapes raise stakes at Biosphere 2. Science, 338, 1417. Summerville, K. S., & Crist, T. O. (2001). Effects of experimental habitat fragmentation on patch use by butterflies and skippers (Lepidoptera). Ecology, 82, 1360. https://doi.org/10.2307/2679995 Summerville, K. S., Veech, J. A., & Crist, T. O. (2002). Does variation in patch use among butterfly species contribute to nestedness at fine spatial scales? Oikos, 97, 195–204. https://doi. org/10.1034/j.1600-­0706.2002.970205.x Tilman, D. (2009). Secondary succession and the pattern of plant dominance along experimental nitrogen gradients. Ecological Mongraphs, 57, 190–214. Vogel, A., Manning, P., Cadotte, M. W., et al. (2019). Lost in trait space: Species-poor communities are inflexible in properties that drive ecosystem functioning. Advances in Ecological Research, 61, 91–131. Watling, J., Arroyo-Rodriguez, V., Pfeifer, M., et al. (2020). Support for the habitat amount hypothesis from a global synthesis of species density studies. Ecology Letters, 23, 674–681. Weisser, W. W., Roscher, C., Meyer, S. T., et al. (2017). Biodiversity effects on ecosystem functioning in a 15-year grassland experiment: Patterns, mechanisms, and open questions. Basic and Applied Ecology, 23, 1–73. https://doi.org/10.1016/j.baae.2017.06.002 With, K.  A. (1997). The application of neutral landscape models in conservation biology. Conservation Biology, 11, 1069–1080. With, K. A. (2016). Are landscapes more than the sum of their patches? Landscape Ecology, 31, 969–980. https://doi.org/10.1007/s10980-­015-­0328-­8 With, K. A., Cadaret, S. J., & Davis, C. (1999). Movement responses to patch structure in experimental fractal landscapes. Ecology, 80, 1340–1353. https://doi.org/10.1890/0012-­9658(199 9)080[1340:MRTPSI]2.0.CO;2 With, K. A., & Pavuk, D. M. (2011). Habitat area trumps fragmentation effects on arthropods in an experimental landscape system. Landscape Ecology, 26, 1035–1048. https://doi.org/10.1007/ s10980-­011-­9627-­x With, K.  A., & Pavuk, D.  M. (2019). Habitat configuration matters when evaluating habitat-­ area effects on host–parasitoid interactions. Ecosphere, 10, e02604. https://doi.org/10.1002/ ecs2.2604 With, K. A., & Pavuk, D. M. (2012). Direct versus indirect effects of habitat fragmentation on community patterns in experimental landscapes. Oecologia, 170, 517–528. https://doi.org/10.1007/ s00442-­012-­2325-­9 With, K. A., Pavuk, D. M., Worchuck, J. L., et al. (2002). Threshold effects of landscape structure on biological control in agroecosystems. Ecological Applications, 12, 52–65. https://doi.org/1 0.1890/1051-­0761(2002)012[0052:TEOLSO]2.0.CO;2 Yao, J., Holt, R., Rich, P., et al. (1999). Woody plant colonization in an experimentally fragmented habitat. Ecography, 22, 715–728.

Chapter 8

Mesocosms

Curiouser and curiouser! – Alice in Wonderland

8.1  What Are Mesocosm Experiments? A mesocosm experiment is an experimental design in which the researcher makes use of contained experiments distributed across a study area. These generally consist of experiments within bounded containers, such as pails, bins, or aquaria, usually in an outdoor setting. The contents of the mesocosm represent a subset of a larger system, for example a plastic container filled with soil from the surrounding environment, or a wading pool filled with lake water (Srivastava et al., 2004). The use of mesocosm experiments goes back decades, particularly in research related to population and community ecology of lakes and wetlands. Earlier work on “container ecology” called these systems “microcosms” (e.g., Beyers & Odum, 1993), and some texts have used the terms microcosm, mesocosm and macrocosm to distinguish between container experiments in small vs. medium vs. large containers (Martin, 2001; Naeem, 2001). However, more recently Srivastava et al. (2004) distinguished microcosms and mesocosms from each other in that both are contained systems, but mesocosms describe containers that are artificially constructed while microcosms are naturally occurring units that are distinct from their surrounding (e.g., tide pools, pitcher plants). We will adhere to this definition and discuss microcosm experiments in the next chapter. Table 8.1 outlines the attributes we are using to discriminate between mesocosms and microcosm (as well as micro-landscapes, which I discuss in Chap. 11). Mesocosm experiments are appealing because they offer precise manipulative control over the factors of interest, but still capture aspects of the natural world. As “mini labs” embedded in the natural world, they all fall under Jenerette and Shen’s (2012) Type II.3 (in situ experiments distributed throughout a landscape). Although much of the published literature using mesocosm experiments tests questions in © Springer Nature Switzerland AG 2022 Y. F. Wiersma, Experimental Landscape Ecology, Landscape Series 29, https://doi.org/10.1007/978-3-030-95189-4_8

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Table 8.1  Characteristics used in this book to distinguish between mesocosms, microcosms and micro-landscapes as experimental systems Container material Experimental setting Inter-patch connections Container contents

Mesocosm Artificial Natural Physical OR via translocations Assembled by researcher OR natural

Microcosm Natural Natural Physical, if at all Natural

Micro-landscape Artificial Laboratory Physical Assembled by researcher

Table 8.2  Taxonomy of types of landscape experiments (sensu Jenerette & Shen, 2012), with bold font in the example column indicating the type of experiment for which mesocosm experiments are especially-well suited, and italic font  for those types which it may be possible to harness mesocosms, but for which other experimental approaches may be better suited. References describing examples of mesocosm experiments of each type are given; these are not exhaustive Group I. Identification of landscape structure

Type of experiment 1. Perception experiment 2. Tracer experiments

II. Identification of process variation within landscapes

III. Identification of process sensitivity to landscape structure

IV. Identification of landscape pattern formation factors

3. In situ experiments distributed throughout a landscape 4. Ex situ experiments using samples collected throughout a landscape 5. Translocation experiments 6. Transport manipulations 7. Manipulation of internal patch characteristics 8. Manipulation of patch shape 9. Manipulation of patch connectivity 10. Fragmentation experiments 11. Manipulation of landscape scale 12. Construction of entire landscapes 13. Manipulative disturbances 14. Vector manipulations

Example Sievers et al. (2018) Baines and McCauley (2018) Paudel et al. (2015)

Gavazov et al. (2014) Stoler and Relyea (2011) Pitcher and Soluk (2016)

Legrand et al. (2015)

15. Self-organization experiments

physiological, population, community and ecosystem ecology, mesocosm experiments can be harnessed to be used for many other types of landscape experiments (Table 8.2) and should be viewed as more than just distributed experiments. When examined against our criteria of good experimental design as outlined in Chap. 2, mesocosm experiments can check all the boxes. There are different strategies to apply a control, as we will see in the case examples, but the “mini

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laboratories” represented by each container makes it highly feasible for the experimenter to implement quite rigorous controls. The size of the containers can make replication easy (although experimenters need to be cautious of not treating the containers as pseudoreplicates; see Chap. 4). The portability of the experimental environments in artificial containers means that it is relatively easy to randomize the placement of the treatments between containers. However, there can be trade-offs for the relative ease of carrying out a randomized, fully replicated experiment with suitable controls. One challenge is that of scaling effects (Petersen et  al., 1999, 2003), meaning it can be challenging to extrapolate from these small, artificial environments to the real world at large spatial and temporal extents. The other is that mesocosms may not fully represent reality (Focks, 2014; Petersen et  al., 2003; Sagarin et al., 2016; Zuk & Travisano, 2018). Mesocosms may exclude predators (although sometimes predator exclusion is the intended treatment to test a particular hypothesis, e.g., Maezono et  al., 2005), or the containers themselves may create biotic or abiotic conditions that are not representative of the larger ecosystem. For example, in aquatic mesocosms, a frequent challenge is accumulation of biofilms on the tank walls, which can increase the amount of primary production beyond what one might expect to find in a similar volume of water in a natural lake or pond (Petersen et al., 1999). Others have demonstrated that walled mesocosms can affect natural predatory behaviour in jellyfish (Martin, 2001) or that walls in smaller mesocosms affected the distribution and swimming behaviour of moon jelly Aurelia, with a disproportionate number adhering to walls (Martin, 2001). In a careful experiment to assess mesocosm effects, Skelly (2002) compared the response of spring peeper (Pseudacris cruifer) larvae to different densities of wood frog (Rana sylvatica) larvae in both artificial mesocosms (plastic cattle watering tanks 152 cm in diameter) and in caged enclosures of the same bottom surface area submerged in natural ponds. They found that the spring peeper densities, growth, and survival decreased with increased wood frog larval densities, but only in the mesocosms, and not when the experimental densities happened in field conditions (the mesh enclosures). They concluded that one cannot always assume that mesocosm experiments represent realistic conditions (Skelly, 2002). Chalcraft et  al. (2005) critiqued Skelly’s (2002) experimental design for not considering all possible factors that explained the difference between the two experimental venues, for example the water source, litter composition and canopy cover, as well as potential lack of independence by having multiple enclosures within one pond. They suggested that carefully-designed mesocosm experiments have value, and can complement field studies (Chalcraft et al., 2005). In a rebuttal, Skelly (2005) countered that conflicts about the benefits and trade-offs between different experimental venues can best be resolved via experiments such as his. The overall message then is that researchers should be mindful of how “cage effects” or “tank effects” may confound results, sometimes in unanticipated and unexpected ways. The use of experimental mesocosms dates back to the early 1960s (Pilson & Nixon, 1980). Many of these early experiments were focused in aquatic/marine systems, perhaps owing to the widespread hobby of fish aquaria (Beyers & Odum, 1993). These began as simple containers ranging is size from 1 L glass carboys to

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1300 m3 (1.3 million L) tanks, and evolved into more complex systems that mimic natural light, turbulence and flow patterns (Pilson & Nixon, 1980). In terrestrial systems, early mesocosm experiments from the late 1970s focused on soil processes, microbial dynamics, plant/water relations, metabolic pathways (with applications for studies of bioaccumulation), trophic relationships, and ecosystem functioning (Ausmus et  al., 1980). An early text on mesocosm experiments suggested that all such experiments had to originate from natural systems and be isolated and compact subsets from the natural ecosystem (Beyers & Odum, 1993). Because they originated from natural systems, mesocosms could also be characterised as being representative of taxonomic, genetic and landscape diversity. Initially mesocosms were described as “low cost” (Beyers & Odum, 1993: p. 6), but this characteristic does not always hold true. Today, highly sophisticated systems, such as the Metatron facility in France (Haddad, 2012) allow for very precise control of artificial environments. As well, the nature of mesocosm experimental designs changes continually. Focusing specifically on stream mesocosm experiments, Menczelesz et al. (2020) found that over time, the size of the mesocosms decreased, and the number and complexity of the experiments (i.e., number of treatments) increased, as did the number of replicates. Ecologists use mesocosms in all sub-­ disciplines of ecology, and there are many resources available for students designing such experiments. In this chapter, I will focus on how researchers have harnessed mesocosms to address spatial/landscape questions, and I will illustrate this using experiments that range from simple and inexpensive to more costly and complex.

8.2  Advantages and Disadvantages of Mesocosm Experiments 8.2.1  Advantages Mesocosms, as suggested above, can be relatively inexpensive. Readily available, low-cost items, such as plastic buckets, rubberized totes or glass aquaria all make suitable containers for mesocosms. The smaller extent of mesocosm experiments generally means that the study area in which they need to be distributed need not be as large as the study areas we saw in the previous two chapters. This offers more venues for researchers to carry out mesocosm experiments. As well, monitoring and maintaining them is logistically simpler if each experimental unit is several metres as opposed to several kilometres apart. Effective experimental design is also easier in mesocosms than in large-scale manipulations (Chap. 6) or experimental model landscapes (Chap. 7). In the latter two chapters, we saw that it could be tricky to distribute treatments randomly, owing to the natural heterogeneity in the systems, especially in the large-scale manipulative experiments. It is much easier to position containers within a smaller extent in a fully randomized fashion. As well, because the experimenter controls what goes into the container, and what happens to it, they

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can more easily control for outside effects. This is much harder to do when a treatment block is several hectares in size.

8.2.2  Disadvantages Not all mesocosms are low-cost; the Ecotron facility at Silwood Park in the United Kingdom (which has not  yet been used for spatial/landscape questions) cited an initial building cost (in 1990s dollars) of US$1.5 million and annual operating costs of over US$100,000 (Lawton, 1996). More recently built ecotron facilities have cost an average of 6 Million Euro (~US$7 M) to build and 140,000 Euro (~US$161,000) per year to run (Roy et al., 2021). The cost of these facilities can limit replication of experimental units to be less than what is feasible with a “buckets-in-a-field” approach. While ecotrons have some elements of realism, they do not capture all the complexity of the natural world, which may compromise external validity (Roy et al., 2021). Mesocosms are not the solution for all types of experiments in landscape ecology. Because they are inherently small experiments, there are questions about scaling-­up the findings from mesocosms to larger landscape extents (Schneider et al., 1997; Petersen et  al., 1999, 2003). As well, many environments (notably marine ones) are influenced by large-scale processes, and enclosing a subset of the ecosystem in a mesocosm may create unrealistic conditions, making inference to larger extents challenging (Sagarin et al., 2016; Skelly, 2002). Petersen et al. (1999) carried out a quantitative literature review of research using aquatic mesocosms. They stressed the need to discriminate between ‘fundamental effects of scale’ and ‘scaling effects’ (Petersen et al., 1999, p. 4). The former are ecological patterns that will hold true in natural systems and at larger scales, while the latter are results that are simply artifacts of the enclosed experiment. They suggested that researchers could carry out multi-scale experiments that systemically change both spatial and temporal scale. They cite several examples of mesocosm experiments that have done this, but none of these focused on landscape ecology questions. However, Sagarin et al. (2016) caution that as mesocosm studies increase in size, they trade-off the ability to replicate, as well as carrying increased complexity in terms of logistics and costs. Alternatively, researchers can take a comparative approach – either by deliberately comparing their mesocosm experiment to patterns in the natural world (“natural experiments”), or to findings in the broader literature. Jiang and Mitsch (2020) took this approach in a “wetlaculture” experiment that examined using wetlands to recycling excess nutrients from agriculture. They compared nitrogen removal in 28 mesocosms (1  m3 in volume) that manipulated water depth and hydrologic flow. They further compared the total nitrogen to the nitrogen loading in nearby experimental wetland areas (10  ha) and found significant scale effects. However, Pace (2001) cautions that being lax about the ultimate scales of interest can lead to “soft extrapolation” which can be erroneous.

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I would offer a further suggestion, which would be to adopt a variety of experimental approaches that test the same hypotheses (for an excellent essay illustrating this in community ecology, see Werner, 1998). For example, a mesocosm experiment could be set up that mimics a large-scale manipulative experiment, but using appropriately scaled taxa. If the patterns hold in both, then the researcher has more confidence that the treatment effect is scale-invariant. Another possibility is to combine in silico models with data from mesocosms. Hammill et  al. (2018) did this when they generated diversity data in situ with field mesocosms, and then used these data to parameterize a simulation model. Others have suggested tools that can effectively extrapolate data across scales, such as Artificial Neural Networks (Magierowski et al., 2015). Finally, researchers should be cautious whenever they distribute the experimental treatments across containers. If one does not properly estimate the within-group variance for the replicates to account for how the random effects contribute to the error term, then there is a higher risk of committing a Type I error via pseudoreplication. When the researchers treat the replicate containers as fixed effects in a statistical test, then they are limited to making inferences only about the specific containers in their experiments, and cannot confidently generalize beyond the experiment. Chapter 4 discusses the issue of pseudoreplication in more detail; anyone planning a mesocosm experiment should carefully review this chapter and the associated resources. For example, in the wetlaculture study, Jiang and Mitsch (2020) carried out a one-way ANOVA followed by a t-test to assess how water level and flow rate affected nutrients. The 28 replicate mesocosms across the 2  ×  2 factor treatment design were not treated as random effects. Thus, their inference is limited to the mesocosms. Because they saw similar patterns in the parallel experiment at the larger extent, their overall findings at the two spatial extents are consistent with their hypothesis that hydrological conditions affect nutrient retention in a freshwater wetland and their finding that a long duration of standing water could lead to phosphorous release and nitrogen removal from the soil. Thus, they have compelling evidence (but not the statistical power to test directly) to infer that the patterns in the mesocosms can be applied to the larger wetland system.

8.3  Case Examples Unlike the previous two chapters, where I organized the case studies by ecosystem type (Chap. 6) or location of model landscape (Chap. 7), the specific material out of which the mesocosm is constructed matters less than the broader question. As mentioned above, many mesocosm studies have focused explicitly on questions in population and community ecology. In his summary of the first suite of experiments at the Ecotron at Silwood Park, Lawton (1996) stated that the small scale of mesocosms made them unsuitable for addressing landscape ecology questions. There is now a wide array of ecotron facilities globally (see Roy et  al., 2021 for an

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overview), and it may be possible to harness these for landscape-ecology research. However, there are examples of mesocosm studies that treat space either implicitly or explicitly, and therefore should be of interest to landscape ecologists. I have grouped these by experiment type, following the taxonomy developed by Jenerette and Shen (2012).

8.3.1  Perception Experiments (Experiment Type I.1) Sievers et  al. (2018) used mesocosms that mimic stormwater wetlands to assess whether the contamination levels of such wetlands (which are common in urban areas) created ecological traps for frogs. They hypothesized that those wetlands with high contaminant levels might negatively affect the fitness and behaviour of tadpoles, and hence be ecological traps. Their experiment consisted of eight replicates of six stormwater wetlands in 48 mesocosms (150 L each in size). They created these by taking sediment and water from the sources wetlands, and paired them by high- and low-contaminant levels. They released tadpoles captured from a common source separate from the stormwater wetlands under analysis, and measured their survival, size at metamorphosis, and development rate. They found significant differences in all fitness metrics between the wetlands with high vs. low contamination levels. Thus, the experiment is an example of an assessment of how tadpoles perceive these stormwater wetlands, which can be a valuable feature in urban environments that jointly provide habitat and control flooding (Sievers et al., 2018). In a spatially-explicit examination of patch quality, Resetarits and Silberbush (2016) used mesocosms to assess how patch quality in terms of presence of predators both within patches and in nearby patches affects selection. Their experimental design used arrays of three experimental conditions (which they termed ‘localities’), each of which had three rectangular plastic pools (51 L). They added predatory fish as the experimental treatment to none, one or two of the 3 tanks in each locality, and replicated the array six times within a fenced experimental research site (Resetarits & Silberbush, 2016). Spacing between tanks in a locality and between localities within an array were such that the full suite of experimental treatments in an array were within the range of perception of female mosquitoes. They assessed whether the rate of oviposition of eggs by female mosquitos (genus Culex) varied based on the patch context in terms of predator presence. If female mosquitos can use chemical cues to detect presence of predatory fish, then they may preferentially select localities within an array where all three tanks had fish absent, or within a locality, they may avoid the tank(s) with fish and deposit eggs in the fish-free tank (Resetarits & Silberbush, 2016). The spatially explicit manipulation of both patch quality and context allows for an assessment of how both of these factors interact and influence how the female mosquito perceives the patch. In a similar experiment, but using colonizing beetles instead of mosquitos, Resetarits (2018) placed fish-free target mesocosms (cattle tanks 1 m in diameter) along two “spoke” transects at 90° from each other spaced 1 m apart with a larger

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(2.7 m diameter) cattle tank containing predatory fish at the “hub”. This allowed him to test how distance from a patch containing a predator affected beetle colonization. In this particular experiment, (Resetarits, 2018) found different responses to perceived risk by different beetle species. Similar experiments on the interaction between patch quality and spatial context can also manipulate patch quality in terms of an attractor (e.g., resource availability) rather than via the deterrent of a predator (e.g., Pintar & Resetarits, 2017).

8.3.2  Tracer Experiments (Experiment Type I.2) Mesocosm treatments generally manipulate the internal environment in some way. In landscape ecology studies, we usually think of this as a manipulation of some aspect of patch- or landscape pattern. However, in a study of the lesser grain borer, a beetle that is often associated with stored grain, Cordeiro et al. (2018) kept the mesocosms homogenous, to mimic the landscape the beetle exploits in a bag of grain, and manipulated the social landscape. They wanted to assess how beetle foraging changed the landscape pattern, and how the social landscape, manipulated by introducing conspecifics of the same or opposite sex, affected foraging behaviour and the resultant patch pattern. The mesocosms were very small glass plates (40 cm × 20 cm) with a 5 mm gap to hold a layer of wheat grains. The researchers traced the movement of beetles within the landscape by marking them with coloured ink, and compared the foraging pattern created when the mesocosm contained a single beetle vs. a second beetle of the same or opposite sex. They found that movements differed by sex, but that for both, the distribution of feeding sites was clumped at smaller scales, and random at the largest scale (entire mesocosm), and their space-use patterns were affected by the presence of a beetle of the opposite sex, increasing the clumpiness of the foraging patches (Cordeiro et al., 2018). The stormwater mesocosm experiment discussed above (Sievers et  al., 2018), also had a tracer experiment. The experimenters placed three pairs of 100 L mesocosms (fiberglass ponds) around each of the six source wetlands. They created each mesocosm by transferring water and sediment from the six source wetlands. Sievers et al. (2018) monitored for oviposition of frog eggs from the source wetland, to trace whether frogs selected to lay eggs in the mesocosm that matched their source pond, or in a pond that had different contamination levels. They did not find any difference in egg masses in the experimental ponds. Thus while the tadpoles appeared to perceive differences in habitat quality in the mesocosms (based on different fitness metrics), tracing frog movement by means of egg masses from source ponds to mesocosms suggested that movement between mesocosms was not affected by mesocosm quality. In a similar experiment that looked at how habitat quality might affect dispersal, Baines and McCauley (2018) transferred adult backswimmers (a type of aquatic insect) from high-quality and low-quality environments into one of 18 tank mesocosms (19  L each) that were created to simulate one of three different levels of

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habitat quality, manipulated through food availability. They marked the backs of the backswimmers with a 4-digit code in permanent marker in order to be able to detect if there was a difference in the dispersal or mortality rate between the mesocosms (Baines & McCauley, 2018). They found that the quality of the habitat that the backswimmers originated from had a significant effect of whether or not they dispersed from the mesocosms (those who grew up in the high-quality habitat were more likely to disperse), but the quality of the destination mesocosm did not. Conducting tracer experiments with mesocosms can allow for a high detection rate of movement of the organisms or element of interest. Tracer experiments in a landscape-scale manipulative experiment will use unique ID tags in mark-recapture studies (e.g., Brinkerhoff et al., 2005), telemetry devices (e.g., Rocha et al., 2017), or distributed camera traps (e.g., Deere et al., 2020) to monitor movement of individuals. Researchers can also use isotopic markers to trace movement of water or elements (e.g., Wang et al., 2019). These methods can be logistically challenging over a kilometres-extent landscape, and often data on the movements of individuals are incomplete or lost. For example, Deere et al. (2020) reported loss of data from their camera traps due to theft, vandalism, and animal damage. Because researchers can monitor mesocosms more closely, due to their smaller size, and because the organisms within them move smaller distances, it is easier to detect and document all movements, and thus make better inferences about how the manipulated factors affect the dispersal of the feature under study.

8.3.3  In Situ Experiments (Experiment Type II.3) All kinds of mesocosm experiments can meet Jenerette and Shen’s (2012) description of an in situ experiment distributed throughout a landscape. Some of these add additional, complementary experiments, a tactic recommended by Jenerette and Shen (2012). For example Paudel et al. (2015), distributed 3360 litter bags across a large disturbance gradient. The litter bags are not mesocosm experiments, but the researchers complemented these with a mesocosm experiment consisting of a 20 m × 20 m shade house in which nine blocks were established with litter and soil collected from the field sites. The nine plots in the mesocosm were exposed to different levels of shading and litter bags similar to the ones deployed in the field (Paudel et al., 2015). Thus, the mesocosm adds an additional level of experimental control to the distributed experiment. The experimental shade house allowed an assessment of how litter and soil characteristics and shading affected decomposition rates, while holding microclimate constant and exposing the plots to a controlled level of sunlight exposure. Thus, the findings complement the distributed experiment, where manipulation of shading would be logistically difficult and where microclimate would not be constant.

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8.3.4  Translocation (Experiment Type II.5) By definition, mesocosms are subsets of the surrounding natural system, often created by moving components from the natural system into the containers. This attribute of mesocosms also means they are amenable to translocation experiments. For example, Gavazov et  al. (2014) transferred turf mesocosms from different land cover types that represented different management intensities along an altitudinal gradient. The researchers relocated the mesocosms to different altitudes from which they originated (keeping one set at the same altitude where the turfs originated), as a way to simulate changing climate. This allowed them to assess how each land cover type might respond to climate change. Moving turf mesocosms upslope or downslope has advantages over answering this kind of question using other experimental approaches. For example, a large-scale manipulation or model to assess climatic gradients is not feasible, although there have been many small-scale manipulative experiments (see meta-analysis of over one thousand of these in Song et al., 2019). An observational study of different land cover types at different altitudes and different sites with different land covers types might elucidate some insights, but it could be difficult to find all land-covers at all altitudes. Moreover, in an observational study it is difficult to tease out the variation due to natural site variability against the factor of interest (in this case altitude).

8.3.5  Internal Patch Characteristics (Experiment Type III.7) Because mesocosms are small, contained patches embedded in the surrounding environment, it is quite straightforward to carry out experiments that manipulate internal patch characteristics. Some of the experiments described in Sect. 8.3.1 above (Pintar & Resetarits, 2017; Resetarits, 2018; Resetarits & Silberbush, 2016), manipulate internal patch characteristics and spatial context in creative ways. There are many examples of manipulation of patch quality in aquatic mesocosms. For example, in a wetland mesocosm experiment, Stoler and Relyea (2011) filled 100 L plastic wading pools with one of 15 different types of leaf litter to assess how the leaf litter inputs affect the wetland community composition. They replicated each treatment four times (60 wading pools in total), and found that, over time, the type of leaf litter used affected phytoplankton density only when Norway spruce was the litter material. However, they observed significant statistical differences in the effect of litter type (they had 11 different broadleaved and coniferous species in their treatments) on periphyton and amphibian biomass (Stoler & Relyea, 2011). This is an example of changing the patch characteristics via the impact of the biotic inputs of different types of leaf litter on abiotic conditions that support life in the wetlands. Other studies have manipulated predator densities as an attribute of patch quality (e.g., Kraus & Vonesh, 2010; Resetarits, 2018; Resetarits & Silberbush, 2016). The backswimmer experiment described above (Baines & McCauley, 2018), also could

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be considered an experiment that manipulated patch quality, but the focus was more on tracing which individuals dispersed from the different patches than it was on how different levels of patch quality might attract different individuals. Many mesocosm experiments that test the effect of nutrient addition on community biodiversity and/or biomass would be examples of patch quality manipulations, even if the underlying research questions are not explicitly spatial. For example, Masese et  al. (2020) added cattle and wild hippopotamus dung in six treatment combinations to experimental mesocosms to see what the effect might be on nutrient inputs into aquatic ecosystems, and Suski et  al. (2018) examined how mesocosms treated with a management regime (application of a pesticide-dye combination) intended to control algal blooms would vary in species diversity. We can also consider experimental warming in mesocosms (e.g., Bridgham et al., 1999) as a type of patch quality manipulation. Such research questions work well in mesocosms. They differ from experiments that manipulate the characteristics of patches embedded in real landscapes, such as the Teakettle or SAFE experiments that manipulated within-patch disturbance (e.g., Bernard et  al., 2016; Cusack et  al., 2015; Goodwin et al., 2018; Luke et al., 2014), or manipulations that control the level of grazing (e.g., Groffman & Turner, 1995; Kay et al., 2017). In the mesocosm experiments, there is less direct interaction (sometimes none) between the patch and the surrounding landscape matrix than in the large-scale manipulations. Thus for questions about patch effects, a large-scale manipulative experiment may have advantages over mesocosm experiments in a landscape ecology context because in the real world, patches are never completely isolated from their surrounding landscape matrix. On the other hand, if researchers want to isolate within-patch effects without having confounding influence from the matrix, then a mesocosm experiment like the ones describe here may be suitable.

8.3.6  Patch Connectivity (Experiment Type III.9) Although the definition of mesocosms as containers that capture subsets of the surrounding ecosystem implies that they are fully isolated (and often they are), mesocosms can sometime be deliberately connected to address questions about patch connectivity. They need not be physically connected either. In the experiments on the effect of chemicals to control algal blooms on wetland biodiversity, Suski et al. (2018) also tested the effect of dispersal on the pond zooplankton communities. They did this by physically transporting zooplankton from natural wetlands to half of the experimental mesocosms, which is a way to “connect” the experimental mesocosms to the natural environment, but in a controlled fashion. Baines et  al. (2020) carried out a similar method in a follow-up experiment with backswimmers in pond mesocosms. They marked the backs of them with unique ID numbers and used mark-recapture to document dispersal between mesocosms. In some mesocosm experiments, researchers connect the patches physically instead of via facilitated dispersal of individuals as in the examples above. In a pond

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mesocosm study of how structural complexity and functional connectivity affected predation rates by dragonfly larvae and a fish predator, Pitcher and Soluk (2016) manipulated habitat connectivity simply by connecting the two mesocosms (320 L plastic trashcans) with PVC pipe of two different lengths (Fig. 8.1). Other types of mesocosms require different tools to experimentally manipulate connectivity between patches For example, Väisänen et al. (2020) used soil mesocosms to investigate how abiotic and biotic components affect soil carbon under climate change scenarios (Fig. 8.2). They wished to isolate biotic from abiotic interactions between permafrost and the active soil layer in mesocosms consisting of the two soil types as a layer in an acrylic plastic box. The researchers manipulated the connectivity between the two layers, and then placed the mesocosms in nine spatial blocks over a 1  km2 study area. To manipulate connectivity of the layers and exchange of abiotic (e.g., water and soil solutes) and different kinds of biotic soil components (microorganisms, fungi, arthropods, worms and fine root matter), they separated the layers using one of five treatments. These were: a plastic wall (full barrier), a 2-mm mesh that allowed exchange of worms and fine root matter, a 20-μm mesh (to allow exchange of fungi and bacteria in addition to the material with the 2-mm mesh), a 20-μm mesh supplemented by inoculation of microarthropods, and a 0.5-μm mesh (biotic exchanges limited only to micro prokaryotes, and abiotic exchange permitted). In a similar experimental set-up, Dettweiler-Robinson et al. (2020) used two types of mesh in biocrust mesocosms, to control interaction between the biocrust, soil fungi and surrounding root matter in order to assess how fungal connections between the biocrusts and roots affected productivity, particularly when the system was stressed by experimentally-induced droughts. The contained nature of mesocosms also means that researchers can more tightly control the connections between patches than in a kilometres-extent landscape. For example, researchers may build a highway over- or under-pass to promote movement of certain species from one patch to another. While these are generally

Fig. 8.1  Diagram of the mesocosm set up (one replicate) used by Pitcher and Soluk (2016). The length of the PVC pipe connecting the two barrels (“patches”) is experimentally varied to see how length affects crossing events by predators between the two patches. (Figure is licensed  under Creative Commons Attribution License CC BY 4.0)

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(b)

(c)

40 cm

Ø 5 mm

Fig. 8.2  Diagram of the mesocosm set up (one replicate) used by Väisänen et al. (2020). Panel a shows the dimensions of the mesocosm, which is divided into a smaller permafrost compartment and a larger active layer compartment. Panel b shows the actual mesocosm, which is made of acrylic plastic. The treatment manipulates the barrier between the compartments; the left-hand image shows a solid barrier (hermetic treatment) and the right-hand photo shows the 2 mm mesh treatment. Pancel c shows the mesocosm with the active layer compartment filled with peat sod and mosses on the left side and the permafrost compartment filled with Styrofoam as an inert substance and recently thawed and homogenized permafrost soil next to the mesh barrier. (Reproduced from Väisänen et al. (2020) and used here with permission from Elsevier)

constructed based on prior analysis of road kills and patterns of topography and landcover (e.g., Gunson et al., 2011), once they are in place, it is nearly impossible to change them to refine an experiment about whether they are as effective as possible. Moreover, structural connectivity may not relate to functional connectivity in clear ways when examining the issue of connectivity in a complex, large-extent system (Cosgrove et al., 2018; Kadoya, 2009). In mesocosms, it is much easier to manipulate structural connectivity rigorously (with controls and replication) and to monitor the effect on functional connectivity for the organisms in the mesocosm. How well this can be extrapolated to connectivity at larger extents is currently not well known, but as we have seen, results from mesocosm experiments, when corroborated by other types of experiments (e.g., observational experiments, large-­ scale experiments, simulation models) increase our overall understanding of the impacts of variation in connectivity on ecological processes and patterns.

8.3.7  Vector Manipulation (Experiment Type IV.14) As with the examples of the mechanisms for manipulating connectivity in the previous section, it is possible to carry out vector manipulation in various ways in mesocosm experiments. Many of these use connected mesocosms—for example, in a butterfly experiment in the Metatron facility, Legrand et al. (2015) connected pairs of cages with identical S-shaped tunnels. Instead of manipulating the length or type of connection, they manipulated the habitat quality in either the origin cage or the destination cage. Because navigating the tunnel was challenging for butterflies, the researchers could test how relative differences in habitat quality acted as a vector to influence dispersal. In a similar experiment with mesocosms with identical

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connections but differences between the origin and destination points, Mausbach and Dzialowski (2019) varied the relative degree of disturbance using zebra mussels and assessed the effect on zooplankton dispersal. Vectors can be extremely difficult to manipulate at large scales. In their discussion of landscape ecology experiments, Jenerette and Shen (2012) cite wind tunnel experiments to assess erosion response to fire as a type of vector manipulation. Engineers regularly use wind tunnels as model systems, and there is no reason not to apply models like this to landscape ecology (see Chap. 11). Applying vector manipulation to mesocosms, which can be scaled-down replicas of the natural world, might add a degree of realism to questions about how vectors affect landscape patterns and processes, although with the caveat that these may not scale up quite as expected (Schneider et al., 1997).

8.4  Conclusion Mesocosms are fascinating and exciting experimental tools that can be relatively inexpensive to set up. Ecologists have made use of mesocosms for many types of questions—more commonly in other branches of ecology, or in toxicology, than in landscape ecology. However, as we have seen in this chapter, researchers can harness mesocosms to address a host of different types of landscape ecology questions by adding a spatial dimension to the experimental design. All mesocosms are, by definition, examples of Jenerette and Shen’s (2012) experiment Type II.3 (in situ experiments) which fall under group II, identification of process variation within landscapes. However, mesocosms can be amenable to manipulation of their internal patch characteristics (III.7) and connectivity (III.9). For example, researchers can make experiments spatially explicit or implicit by manipulating the spatial characteristics within the mesocosms (e.g., within-mesocosm patch pattern) or the spatial arrangements between mesocosms (e.g., distances or degree of connectivity between mesocosms). With some creativity, mesocosms are also amenable for perception, tracer and translocation experiments. Many of the experiment types discussed here can also be carried out in microcosms (which will be discussed in the next chapter) and in micro-landscapes (which are discussed in Chap. 11), although, as with all the experimental systems discussed so far, each has different advantages and disadvantages.

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Chapter 9

Microcosms

Our world is made up of a myriad of microcosms, of tiny worlds, each with its own habitues, every one known to the others. ― Louis L’Amour, Education of a Wandering Man

9.1  What Are Microcosm Experiments? In the previous chapter, I introduced mesocosms as a type of experiment in which components of the natural world were contained in human-built physical entities (e.g., plastic tubs, glass aquaria) that researchers use for experimental manipulations within the context of their natural surroundings. Here, I describe a similar, but slightly different type of experiment, that of the microcosm—which I define as an experimental system in which the contained system is naturally occurring (e.g., tide pools, pitcher plants) and replicated across the local environment. Because some literature refers to “container experiments” (those I discuss in Chap. 8) as microcosms, Srivastava et al. (2004) qualify microcosms as “natural microcosms” to distinguish them from experimental systems in artificial containers. The two terms—microcosm and mesocosm—are used in the literature (and in many of the papers cited in both this chapter and the previous one) somewhat interchangeably. However, in this book, I have aligned with Srivastava et  al.’s (2004) division by container type, and delineated microcosms as those contained experiments that occur naturally, and mesocosms as those that occur within artificial containers. See also Table 8.1 in the previous chapter for a list of attributes that I am using to discriminate between the experimental types in this book. Srivastava et al. (2004) provide an excellent review of (natural) microcosms and cite similar advantages for experimentation as discussed in the previous chapter for mesocosms; their small size makes manipulations and replications of experimental treatments very tractable. Moreover, the taxa living in microcosms tend to have short generation times, which means that experimenters can get meaningful responses over a short-term experiment (Srivastava et  al., 2004). Examples of © Springer Nature Switzerland AG 2022 Y. F. Wiersma, Experimental Landscape Ecology, Landscape Series 29, https://doi.org/10.1007/978-3-030-95189-4_9

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microcosms that are naturally bounded systems include rock pools, aquatic food webs in pitcher plants, aquatic insects in bromeliads, and arthropod communities in moss patches on bare rocks. These natural “containers” have the realism of field experiments, but allow the experimenter to carry out controlled experimental manipulations as they might in a lab study. Moreover, unlike some mesocosms that researchers assemble from their surroundings, which may miss key components of the ecological system, the natural subsets of microcosms is more likely to represent the full suite of biodiversity and evolutionary interactions. Thus, this can add increased realism. The fact that microcosms are naturally existing systems in and of themselves is a reason that Srivastava et al. (2004) make the case that they function as a model system for ecological research. Model systems are scaled-down versions of other, more difficult to manipulate, biological systems. In medicine, rats and mice are common model systems for preliminary human drug trials, and the fruit fly, Drosophila melanogaster is a model system in genetics. Model systems usually are smaller, respond faster, and are easier to manipulate than the systems they represent, but are similar enough to larger, slower systems to facilitate inference across scales. Model systems share traits of “being simpler than other systems of its type, so the property of interest is not obscured by others” (Vitousek, 2002, p. 573), and allow for “tractability, generality and realism” (Srivastava et al., 2004, p. 379). In their review, Srivastava et  al. (2004) suggest types of ecological questions for which microcosms might be especially suited that span questions in ecology, including community and ecosystem ecology and metacommunity theory. Although they do not label it as a microcosm, Lindo and Gonzalez (2010) describe the bryosphere as a spatially bounded ecosystem that can function as a model system. Their focus is on questions ranging from molecular to physiological to community and ecosystem ecology, however, some of the characteristics of the bryosphere they describe, such as vertical zonation, have links to concepts in landscape ecology, such as spatial gradients. Much of the discussion of using microcosms as model systems has focused on research in community or ecosystem ecology (Srivastava et  al., 2004; Lindo & Gonzalez, 2010 as discussed above; also see Mammola, 2019 for a review of caves as model ecosystems). However, others have offered different microcosms as candidate model systems that might be specifically well suited for landscape ecology. These model systems can be useful when the scale of the system matches that of a particular landscape process. For example, Bowker et al. (2014) proposed that soil biocrusts (complex microcosms made up of lichens, fungi and bryophytes) are “real landscapes” that are small but have as much diversity within them as larger landscapes or ecosystems. They proposed biocrusts could be good model systems for community, landscape and ecosystem ecology. They have advantages for research in that researchers can easily study them in situ, or via transplanting them to pots for more intensive manipulation under controlled greenhouse experiments (Bowker et al., 2014). In a similar system, Wiersma and McMullin (2018) noted that patches of macro-lichens on the boles of trees resembled patches of land cover as seen from the air, and thus hypothesized that individual trees can be analogs for model

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landscapes. They pointed out that since a stand of trees may be fairly homogenous in certain characteristics (especially if the stand originated at a single point in time, such as following a disturbance), individual trees of the same species and age can function as replicate landscapes.

9.2  Case Examples Because of their similarity in scale and design to mesocosms, many of the same types of experiments discussed in the previous chapter on mesocosms work in microcosms as well (Table 9.1). I have grouped the case examples here in the same way as in the previous chapter, following the experimental taxonomy of Jenerette and Shen (2012) and contrasting the approach (highlighting advantages and disadvantages) of using microcosms vs. mesocosms for each type of experiment.

Table 9.1  Taxonomy of types of landscape experiments (sensu Jenerette & Shen, 2012), with bold font in the example column indicating the type of experiment for which microcosm experiments are especially-well suited, and italic font  for those types which it may be possible to harness mesocosms, but for which other experimental approaches may be better suited. References describing examples of mesocosm experiments of each type are given; these are not exhaustive Group I. Identification of landscape structure

Type of experiment 1. Perception experiment 2. Tracer experiments

II. Identification of process variation within landscapes

3. In situ experiments distributed throughout a landscape 4. Ex situ experiments using samples collected throughout a landscape 5. Translocation experiments 6. Transport manipulations 7. Manipulation of internal patch characteristics 8. Manipulation of patch shape 9. Manipulation of patch connectivity

III. Identification of process sensitivity to landscape structure

10. Fragmentation experiments

IV. Identification of landscape pattern formation factors

11. Manipulation of landscape scale 12. Construction of entire landscapes 13. Manipulative disturbances 14. Vector manipulations 15. Self-organization experiments

Example Munguia (2007) Acevedo and Fletcher (2017)

Petermann et al. (2015) Gilbert et al. (1998) Fletcher et al. (2018)

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9.2.1  Perception Experiment (Experiment Type I.1) Although Jenerette and Shen’s (2012) description of perception experiments emphasizes either human preferences, or animal behavioural responses to landscape patterns, we can think of non-animals as also experiencing preferences to be in one location over another. Microcosms provide one avenue to test these questions experimentally. In their “trees-as-landscapes” model system, Wiersma and McMullin (2018) tested whether the lichen patch pattern on 12 trees that housed a globally rare lichen were significantly different than the pattern on 12 trees along the same 100 m transect that did not have the lichen. They found no difference in landscape patch pattern between the two sets of trees, but small differences in overall lichen abundance (Wiersma & McMullin, 2018). Thus, the rare lichen may “perceive” the landscape of an individual tree to have an attribute that makes it a higher quality habitat than other trees where it is not found, but what this is, is still unknown. A manipulative experiment whereby researchers actively transplanted rare species to other trees and assessed for their survival could help elucidate whether there are habitat quality differences between these microcosms, or whether rare lichen presence is simply random. However, for ethical issues, Wiersma and McMullin (2018) were not able to carry out such a manipulative experiment. In a similar observational study, but using dead pen shells as microcosms, Munguia (2007) examined whether the spatial aggregation of dead pen shells affected the organisms living on them. They found a significant difference between the fauna on the shells vs. in the surrounding seagrass habitat, but the spatial patterning of the shells (at least at the scale they sampled) did not affect the community diversity on the shells themselves. However, they noted some variation in response between motile and sessile species, suggesting differences in how these organisms perceived the surrounding landscape (Munguia, 2007). Using the biocrust microcosm proposed as a model landscape by Bowker et al. (2014), Castillo-Monroy et  al. (2014) carried out experimental manipulations of patch pattern to assess the effect on microbial diversity. They found that microbial communities responded to the spatial patterns of the biocrusts and that microbial diversity increased as patch richness and evenness increased. Although we do not normally consider microbes to exhibit “behaviour”, this is an example of a type of “perceptual” response. Moreover, this study illustrates the potential advantage of a microcosm over a mesocosm for a perceptual experiment focused on microorganisms. In an artificial mesocosm, it may be difficult to control the transfer of microorganisms, or to know what quantity is present, especially if the researcher assumes that microbial organisms are simply transported along with the soil or water into the container. Conversely, in a microcosm, the natural biota, including the microbial component, are already present. When extrapolating findings from perceptual experiments using microcosms to larger extents, a limitation may be the fact that the behaviour of larger taxa is quite different and more complex from the taxa used in microcosm experiments, and that some of the physical environment from the perspective of a small organism may not have realistic analogues at larger extents. Obviously, perceptual experiments with humans, such as landscape preference

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experiments, have the added benefit (and challenge) of being able to interview their test subjects. However, these may not be as easy to manipulate experimentally as microcosm experiments. Moreover, anyone setting out on an experiment that involves interviewing human subjects should make sure to work with colleagues with experience in the proper methods and techniques, as these can be complex.

9.2.2  Tracer Experiments (Experiment Type I.2) As with the mesocosm experiment, researchers can use microcosms to conduct tracer experiments. Acevedo and Fletcher (2017) used permanent marker to mark the back plate of a cactus-feeding insect. The study insect is an obligate dweller of the Opuntia humifusa species of cactus, and moves between patches of cacti by walking between 1–2.5 m/day. Their research traced the insects’ movement between microcosms consisting of patches of a single species of cactus. In the experimental design, the researchers released an insect in the centre of a microcosm, which had four potential destination microcosms made up of cactus pads located 1 m away, in each of the four cardinal directions (Acevedo & Fletcher, 2017). They tested how factors of wind, patch area and conspecifics affected movement by introducing a fan to one side of the microcosms, varying the density of cactus patches between the four directions (while keeping the total area in the microcosm constant), or by either adding a male or female conspecific to one of the destination patches. Acevedo and Fletcher (2017) released 240 individuals, and recaptured 86 of these. The experimental result confirmed the field observations that movement was often asymmetric, and showed that the best explanation was organisms choosing to move from smaller to larger patches, rather than the attractive forces of a conspecific or the influence of wind (Acevedo & Fletcher, 2017). Tracer experiments in microcosms are also possible even when the organism is too small or difficult to mark or re-capture. Schooley and Wiens (2004) followed cactus bugs (Chelinidea vittiger) through a 0.8  ha arena of grass surrounded by patches of its preferred habitat, the cactus Opuntia spp. They traced movement of marked cactus bugs at 1 min intervals for 50 min, and planted numbered flags to record the movement path (flags were placed at 1 min delays to avoid having the researcher affect the movement). In a similar approach, With (1994) used 5 m × 5 m microcosms of grassland vegetation and released one of three species of grasshopper at randomly selected points within the plot. Instead of marking the grasshoppers in a mark-recapture study, as Schooley and Wiens (2004) and Acevedo and Fletcher (2017) did in the above study, With (1994) observed each individual for 30 min. At 20 s intervals, she marked their position with a consecutively numbered toothpick flag and located the coordinates of each toothpick at the end of the observation period. She replicated this for five individuals per species (of three species) across five plots in each of two pastures. That represents 150 individual grasshoppers observed, which would have taken 75  h of observation time! This fine temporal grain of data collection yielded movement data that With (1994) used to analyse the

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fractal dimension of movement pattern and relate to the heterogeneity of the grassland vegetation microcosms to show that they responded to both the microlandscape pattern and the pasture type (which differed in their grazing history). Achieving this kind of fine resolution (every 20 s) movement data on a large mammal would limit the battery and storage capacity of GPS collar, even with time interval for observation scaled to body size. As well, the costs of a GPS collars and deployment greatly exceed the cost of the observer’s time in the landscape. Researchers can also observe movement of smaller organisms within a constrained experimental arena with cameras, a technique that would be difficult to apply at a larger spatial extent. Thus, if a researcher has patience to do tedious work on their hands and knees in a meadow, or watch hours of video, they can do tracer experiments with more detail than might be feasible with larger organisms at kilometre extents.

9.2.3  Internal Patch Characteristics (Experiment Type III.7) Bromeliad microcosms are very amenable to having their internal patch characteristic manipulated, much as we saw for the contents of mesocosm containers. The tightly packed axial leaves of a particular group of bromeliads—the “tank” bromeliads—form a reservoir of water that creates a unique internal environment for arthropods and microorganisms. The contents of these tank bromeliads often contain fauna that are endemic to the internal bromeliad environment and not found in nearby water bodies (Lopez et al., 2009). To assess whether biotic or abiotic conditions inside the tank bromeliads created a limiting environment for these invertebrates, Lopez et al. (2009) replaced their contents with aquatic invertebrates cultured in the lab, but originally sampled from the surrounding environment. They found that organisms from the surrounding pond could survive in small artificial containers, but not in the bromeliads, which suggested that the bromeliads created an environment that was not hospitable to these organisms, but was suitable for the endemics (Lopez et al., 2009). In a similar approach, Petermann et al. (2015) homogenized the contents of 27 experimental bromeliads, and then subjected them to one of three trophic treatments to test for bottom-up effects vs. top-down effects. The researchers tested bottom-up effects by adding resources (leaf litter) to nine of the bromeliads, and top-down effects by adding predators (mosquito larvae). They left the remaining bromeliads as controls, and assessed how community composition changed between bromeliads (patches). While not a spatially explicit question, the ease at which researchers can manipulate the internal environment of bromeliads offers a chance to manipulate patch characteristics with a high degree of replication. It also allows for additional manipulations of the environment surrounding the bromeliad “patch”, as Pires et al. (2017) did in a full-factorial experiment that manipulated litter inputs (7 levels) and rainfall received (5 levels) for a total of 175 experimental units to assess the effect these had on creating algae-dominated conditions inside the tank bromeliads. These manipulations of the natural containers in bromeliad microcosms is one

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way to experiment with internal patch characteristics (Type III.7). It is very similar in its approach as the methods seen for this type of experiment with mesocosms in the previous chapter.

9.2.4  Patch Connectivity (Experiment Type III.9) Just as researchers have tested questions about patch connectivity using corridors in kilometres-extent landscapes (as we saw in the Savannah River studies, in Chap. 6), they can do the same with microcosm patches. Rantalainen et al. (2006) carried out an elegant study with soil humus microcosms (2 cm2) which they created by removing the organic soil layer from 32 square plots 25 cm × 25 cm in size. They then created a square of four fragments of humus microcosms, each 2 cm2, and separated 2.4 cm apart. Half of the plots had a 2.4 × 0.3 cm corridor of humus connecting the four patches to each other. As well, they assessed dispersal of soil fauna by isolating half of the larger plots from the surrounding soil with a plastic sheet barrier wall embedded in the soil, and leaving the other half open (Rantalainen et  al., 2006). They sampled the fragments periodically for diversity of soil fauna. They found that microarthropod abundance declined in the isolated patches (those with the plastic wall), but only when there were also no corridors. Isolated patches connected by corridors had nearly the same abundance of microarthropods as the control (open) patches. In a parallel study, they repeated the experimental design at three scales to assess how isolation and connectivity affected microfauna when the size of the plot, fragments, distance from the surrounding soil and length of the corridors varied (Rantalainen et al., 2005), which is an impressive design. Cross-scale manipulations of patch and corridor size would be much more difficult to carry out, and certainly not as well replicated, in a kilometres-extent landscape. In a similar experiment with scaled-down corridors, Gilbert et al. (1998) created an  experimental patch-corridor treatment on six flat limestone rocks covered in moss. They cleared the moss to create four round patches (each 10 cm in diameter). They then manipulated these four patches with either a corridor connection, a corridor that had a 5 cm gap in the middle, or by leaving them completely unconnected. They sampled four patches of the same size, but which remained embedded in the surrounding moss, as the control, and assessed how the presence or absence of corridors affected the moss fauna after a six-month period (Gilbert et al., 1998). They replicated each of the four treatments six times, once on each rock. They found that patches with broken corridors responded similarly to the completely isolated patches, and that corridors significantly increased faunal richness, but that the patches, even when connected by corridors, had lower diversity than the “mainland” large moss patch. Thus, while patches connected by corridors did not allow for the full suite of species to persist, it did prevent some species from becoming locally extinct from the small patches. In a slightly different experimental design, Gonzalez and Chaeton (2002) replicated seven rocks that each had a large (50 cm × 50 cm) “mainland” moss patch which was surrounded by twelve 10 cm2 circular fragments

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that were either connected by a corridor, a broken corridor (2–3 cm gap) or fully isolated (7 cm gap). After six months, they found no difference in species richness between the mainland patch and the small patches connected by corridors. This difference in outcomes between the Gonzalez and Chaneton (2002) and Gilbert et al. (1998) experiments illustrates the importance of applying similar experimental approaches in different contexts. Because each landscape and group of fauna are unique, broader understanding and development of theory or conceptual frameworks is not possible with a limited number of experiments. In this system, further work is necessary to see why in one case patches connected by corridors had the same faunal assemblage as the mainland, while in the other case there was less diversity. Possible reasons could be the local microenvironment, inter-annual differences in environmental conditions, the suite of fauna examined, the number of treatments/replicates, or the size of the mainland, patches and corridors. Åstrom and Part (2013) borrowed the moss-microcosm model of Gonzalez et al. (1998) to carry out a complex, multi-factorial experiment to test the effects of corridors on the faunal community. As with the previous studies (Gilbert et al., 1998; Gonzalez et al., 1998; Gonzalez & Chaneton, 2002), their experimental system consisted of four round patches (100 cm2) that were either connected by narrow corridors, or disconnected. In addition, they manipulated the surrounding matrix, by embedding the patches in either plywood or gravel, and also covered half the landscapes with a mesh roof/watering treatment, which reduced desiccation compared to the other plots. Finally, Åstrom and Part (2013) mimicked Simberloff and Wilson’s (1969) classic defaunation experiments in island biogeography by defaunating one of the patches in each treatment. They found that the presence of corridors had differential effects depending on the taxonomic group, that were counter-intuitive for some—with non-predatory oribatids having higher richness and abundance in the unconnected patches than the connected patches. They also found that the matrix quality (plywood vs. gravel) and environmental conditions (shade/rain treatment vs. open) affected parts of the microarthropod community. Recolonization of the defaunated patches also varied, with predatory species having the lowest recolonization rates. Their study is worth a closer look for its elegant design. They avoided problems of pseudoreplication by using mixed models and reported effect sizes. Connectivity in microcosms is different from those we saw in the mesocosm experiments, where inter-patch connection was either artificial (through physical conduits between containers) or mediated via active transport of individuals between patches. Depending on the nature of the microcosm, building physical connections into the experimental design can be quite easy to do—such as the corridors in the moss microcosms—or can be more challenging—such as with “container” microcosms, such as bromeliads or pitcher plants. In other microcosms such as tide pools, or shells, the patches are inherently always physically isolated from each other and so experimentally connecting them would not be a logical manipulation.

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9.2.5  Fragmentation Experiments (Experiment Type III.10) Fragmentation experiments are somewhat the corollary of connectivity experiments. While we did not see any examples of fragmentation experiments with mesocosms in the previous chapter (perhaps because it is difficult to fragment within an artificial container), Gonzalez et al. (1998) carried out a fragmentation study in the same moss microcosm discussed above. They examined the effect of fragmentation on species richness and abundance in a continuous (50 cm × 50 cm) moss patch and in six 20 cm2 circular fragments (each replicated eight times) that they created by removing moss to leave an inhospitable bare rock matrix (Gonzalez et al., 1998). Twelve months after the experimental fragmentation (sampled every 2 months), they found that abundance declined over time in the fragments (Gonzalez et al., 1998). In a subsequent paper, using the same data, Gonzalez and Chaneton (2002) also tested for the effect of fragmentation on arthropod biomass, in addition to richness and abundance. They found that, as with richness and abundance, arthropod biomass also decreased in the fragments, but was not significant 8 months after the experimental fragmentation had occurred (Gonzalez & Chaneton, 2002). Although Gonzalez et al. (1998) and Gonzalez and Chaneton (2002) labelled their studies as “fragmentation” experiments, the designs do not allow for discrimination between habitat loss and fragmentation per se (Fahrig, 1997, 2013; Jackson & Fahrig, 2016). Nonetheless, one can imagine harnessing moss mesocosms to do this, as with the experiments at Bowling Green (With & Pavuk, 2011). Using the same cactus bug system we saw in the tracer experiments (Schooley & Wiens, 2004; Acevedo & Fletcher, 2017), Fletcher et al. (2018) conducted a fragmentation experiment to assess the effects of random vs. aggregated loss of habitat patches on cactus bug abundance, movement and demographics. They experimented in 15 landscapes, each of which was 50 m × 50 m and had naturally patchy distribution of cacti—the obligate habitat of cactus bug. They left three landscapes as controls and then randomly removed over 2000 patches of cactus across the remaining landscapes, with removal representing 12–94% of patches (leaving between 15–150 patches). They then surveyed all patches every 2 weeks for cactus bug abundance. They found that habitat loss caused declines in cactus bug abundance, with critical thresholds at 70–80% loss of patches. Abundance was higher when patch loss was random compared to aggregated, and this difference was more pronounced at low levels of habitat loss (Fletcher et al., 2018).

9.3  Conclusion For three types of experiments where I discussed examples that used mesocosm experiments in the previous chapter—in situ experiments (Type II.3), translocation experiments (Type II.5) and vector manipulation (Type IV.14)—I was unable to find a corollary that used microcosms here. This discrepancy suggests that microcosms

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and mesocosms are not always interchangeable. Some techniques for manipulating patch characteristics (Type III.7) or tracing movement of arthropods between patches (Type I.2) might be similar between meso- and microcosms. However, the artificial vs. real characteristics of each mean that some types of experiments are more limited to the one approach over the other. Fragmentation experiments (Type III.10) appear to be possible with some kinds of microcosms (notably moss microcosms), but it is difficult to fragment within artificial container mesocosms. Conversely, carrying out translocation experiments (Type II.5) or vector experiments (Type IV.14) may be easier when the container is artificial. In reviewing the literature for this chapter and the previous one, it is clear that the boundaries between what differentiates mesocosm experiments from microcosm experiments are fuzzy, despite my attempt in Table 8.1 to discriminate between them! It certainly does not help that researchers do not use the terms consistently! The humus patch experiments discussed in this chapter (Rantalainen et al., 2005, 2006) are not perfectly contained microcosms per se, as defined by Srivastava et al. (2004) as they were constructed by homogenizing existing humus and redistributing them in patches in bare soil. Similarly the biocrust experiment took patches of biocrust and artificially combined patches and then propagated them in a controlled greenhouse setting (Castillo-Monroy et al., 2014), which makes them a little more like a mesocosm. In another experiment that straddles the microcosm/mesocosm divide, Staddon et al. (2010) harvested moss patches and put them in lab growth chambers (they called them “experimental microcosms” perhaps to differentiate them from “natural microcosms” sensu Srivastava et al. (2004). Staddon et al. (2010) housed the moss patches in sub-chambers connected by PVC pipe in configurations that mimicked the in situ design of the field microcosm experiments discussed above (Gilbert et al., 1998; Gonzalez et al., 1998). They did this in order to control airflow, humidity and temperature between the replicate connectivity treatments. As well, the lab set up allowed them to collect data on CO2 exchange and dissolved organic carbon and total nitrogen collected via leachate out of the sub-chambers, to see how these abiotic factors, in addition to microfauna, responded to the experimental connectivity between the patches. This experiment matches many of the “micro-landscape” experiments reviewed by Larsen and Hargreaves (2020). Because most of the micro-­landscapes discussed by Larsen and Hargreaves (2020) are constructed, either out of natural (e.g., leaf islands) or artificial materials (e.g., well plates), with the experiments carried out in lab settings, they have characteristics of both mesocosms and microcosm. I have decided that because these micro-landscapes are spatially explicit, but do not (for the most part) occur naturally at any scale, that they are “novel landscapes” and I will discuss such experiments in Chap. 11.

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Rantalainen, M. L., Fritze, H., Haimi, J., et al. (2005). Species richness and food web structure of soil decomposer community as affected by the size of habitat fragment and habitat corridors. Global Change Biology, 11, 1614–1627. https://doi.org/10.1111/j.1365-­2486.2005.000999.x Schooley, R. L., & Wiens, J. A. (2004). Movements of cactus bugs: patch transfers, matrix resistance, and edge permeability. Landscape Ecology, 19, 801–810. Simberloff, D. S., & Wilson, E. O. (1969). Experimental zoogeography of islands: The colonization of empty islands. Ecology, 50, 861–879. https://doi.org/10.2307/1934856 Srivastava, D. S., Kolasa, J., Bengtsson, J., et al. (2004). Are natural microcosms useful model systems for ecology? Trends in Ecology & Evolution, 19, 379–384. https://doi.org/10.1016/j. tree.2004.04.010 Staddon, P., Lindo, Z., Crittenden, P. D., et al. (2010). Connectivity, non-random extinction and ecosystem function in experimental metacommunities. Ecology Letters, 13, 543–552. https:// doi.org/10.1111/j.1461-­0248.2010.01450.x Vitousek, P.  M. (2002). Oceanic islands as model systems for ecological studies. Journal of Biogeography, 29, 573–582. https://doi.org/10.1046/j.1365-­2699.2002.00707.x Wiersma, Y.  F., & McMullin, R.  T. (2018). Is it common to be rare on the landscape? A test using a novel model system. Landscape Ecology, 33, 183–195. https://doi.org/10.1007/ s10980-­017-­0599-­3 With, K.  A. (1994). Using fractal analysis to assess how species perceive landscape structure. Landscape Ecology, 9, 25–36. https://doi.org/10.1007/BF00135076 With, K. A., & Pavuk, D. M. (2011) Habitat area trumps fragmentation effects on arthropods in an experimental landscape system. Landscape Ecology, 26, 1035–1048.

Chapter 10

In Silico Experiments

I do not fear computers. I fear lack of them. Isaac Asimov

10.1  Working with Computers The widespread accessibility of desktop computers was coincident with the formalization and early growth of the field of landscape ecology in North America at the Allerton Park workshop in 1983 (Wu, 2013). Ecologists prior to that time would have been familiar with mainframe computers, which many researchers had available to them since the 1960s. In fact, if you ask a landscape ecologist of a certain age about their graduate research, they will regale you with stories about punch cards and trips to “the computer”—a single machine on campus, housed in its own room. Desktop computers for widespread use did not exist until the late 1970s, with the introduction of the Apple II, TRS-80 and Commodore PET. These computers were not very powerful and had limited storage space. To illustrate, the Commodore PET had 8 kB of RAM, and no storage (one had to store files on magnetic tape). It cost US$795 in 1977 dollars (equivalent to US$3475 in 2021). Now, in 2021, I can buy a new, ‘low-end’ laptop for just over US$300 (a tenth of the price) and it will have 4GB of RAM (which represents 4 million times more working memory than the PET) and 128 GB storage capacity. As computer memory and speed increased, with a corresponding drop in price, it became more feasible to do complex computational analysis at one’s desk. By the late 1980s and early 1990s, just as the discipline of landscape ecology was developing in North America, graduate students and university researchers could do complex statistical analysis, mathematical modelling, and GIS analysis right in their own workspace. In a 1988 article in BioScience, Huston et al. (1988) described how then-new computer technology (which would seem primitive by today’s standards) allowed for individual-based models that opened up new avenues for hypothesis testing not previously available. Although their focus was on models of population © Springer Nature Switzerland AG 2022 Y. F. Wiersma, Experimental Landscape Ecology, Landscape Series 29, https://doi.org/10.1007/978-3-030-95189-4_10

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and community-level processes, Huston et  al. (1988) alluded to landscape-type questions when they pointed out that these individual-based models could track variation in individual plants in response to spatial variation. Our discipline was not immune to the increased use of quantitative approaches to ecology; indeed the very first issue of the journal Landscape Ecology contained a paper on neutral models (Gardner et al., 1987) and one describing a spatial simulation (Turner, 1987). Those readers who think experiments involve manipulations and measurements in the field or lab may wonder why I want to discuss computer models and quantitative approaches in a book about experiments. I argue that in silico experiments have just as much validity for testing hypotheses, as do the other experimental approaches discussed in this book. While they are quite different from manipulative experiments in the field or lab, in silico work can meet the criteria of experimental design discussed earlier in this book (control, randomization, and replication), and offers advantages and opportunities that experiments in the real world do not. I am not the only one who thinks so. You can read a more thorough line of argument about complex modelling and its relationships to landscape ecology research in an intriguing paper in Ecological Modelling by Seppelt et al. (2009). This is probably the only time you will find a scientific paper written like the script for a play (in fact, a quote from one of the characters is the epigraph to Chap. 3). The authors imagine a dialogue between two fictional academics: Rebecca, a modeller, and Tony, a practically minded landscape ecologist. In the dialogue (over coffee), Tony argues that Rebecca’s complex mathematical abstractions are too removed from the concrete world of species and landscapes and will do little to address real-world environmental challenges. Through the course of the conversation, Rebecca tries to convince Tony that modelling can help to understand the complexities of the real world and that “the more we deepen our understanding of the interacting processes the more we learn about influencing the environmental systems” (Seppelt et  al., 2009, p. 3482). Tony and Rebecca eventually agree that models “provide a virtual landscape lab for conducting numerical experiments” (Seppelt et al., 2009, p. 3485). I hope that through providing some examples of in silico applications, you can be convinced of this as well. Before we dive into some examples, a few points of clarification are necessary. The term in silico is borrowed from medical research, which distinguishes between in vitro (within glass), in vivo (within a whole, living thing) and in silico experiments. Broadly then, an in silico experiment is any experiment on a computer. In medical research, it can include sequencing techniques, molecular modelling and whole cell simulations. In landscape ecology, in silico work may include (but is not limited to) statistical models, mathematical models, GIS analyses, cellular automata models and agent-based models (Zvoleff & An, 2014). The interdisciplinary nature of landscape ecology means that some landscape ecology research may harness bioinformatics, geomorphological or atmospheric models. One caveat that is particularly germane to models in landscape ecology is how they treat space. While we know that space (and scale) are fundamental to our discipline, not all models treat space the same way. Some ecological models are aspatial, in others; space may be treated implicitly or explicitly (see Chap. 4 and the glossary for a review of these

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terms). Epperson et al. (2010) provide an excellent overview of the development and applications of in silico techniques to landscape genetics, including how— within that sub discipline—early models were aspatial, and have more recently become spatially explicit. Although their in-depth review of specific computer programs is mostly germane to landscape genetics, many of the roles that Epperson et al. (2010) identify for simulations can apply to other branches of landscape ecology as well, including testing model assumptions, characterizing the properties of statistical estimators, and applying models to real systems. When applying in silico models to a research question, it is critically important to consider why you need a model. Verboom and Wamelink (2005) characterize models along two axes: strategic-tactical and mechanistic-descriptive. Strategic models are simple, parsimonious models and serve to lead to general insights, while tactical models are more complex, highly specific and are good at exact predictions for a particular application, but are not generalizable (Verboom & Wamelink, 2005). Mechanistic models mathematically emulate known processes within a system. Although they inevitably simplify reality, they provide an arena to experiment with how variation in input parameters affects the output. Descriptive models quantify the relationship between two variables; this pattern may imply causation, but such mechanisms may not exist in the real world (Verboom & Wamelink, 2005). Other authors describe these model types as mathematical (mechanistic) vs. statistical (descriptive) (e.g., Pelletier et al., 2008; Grant & Bradbury, 2019; Saltelli, 2019). Saltelli (2019) emphasizes the need to consider how trade-offs between model simplicity and complexity affect model error, and suggests a figure that should be prominently hung above every modellers’ desk (reproduced here as Fig. 10.1). Finally, it

Fig. 10.1  The relationship between model complexity and model error. Reproduced with permission from Saltelli (2019) who suggests this figure hang above every modeller’s desk. Models that are too simple may be inadequate and have high model error (red line); however, added complexity can lead to error propagation (blue line). Overall modelling error (green line) is the result of both sources of error. (Used with permission of the author and under CC-BY 4.0 License)

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is always important to validate a model, and assess its accuracy. Related to this, sensitivity and uncertainty analyses are useful steps in modelling that can easily be overlooked (Verboom & Wamelink, 2005; Saltelli, 2019). In a recent manifesto motivated by the relationship between scientific models and public policy in the recent COVID pandemic, Saltelli et al. (2020) outline five key principles that modellers should be mindful of: assumptions (assess uncertainty and sensitivity), hubris (complex is not always better), framing (matching purposes and context), consequences (don’t let numbers drive everything) and unknowns (acknowledge ignorance).

10.1.1  Models in Landscape Ecology Brown et  al. (2006) discuss the use of models in landscape ecology specifically. Echoing the dichotomy between descriptive and mechanistic models (sensu Verboom & Wamelink, 2005), they highlight that the two main reasons for using models in landscape ecology as being for: (1) making inferences about how and why landscapes change (“pattern models”), and (2) predicting future landscape states and patterns (“process models”). In my opinion, there are more reasons than these to use models in landscape ecology. While Saltelli (2019, p. 2) suggests that “(m)odelling hubris may lead to ‘trans-science’, a practice which lends itself to the language and formalism of science but where science cannot provide answers”, I would argue that, when used properly, models can form part of the scientific process. Indeed the pattern-process models illustrated in Fig. 10.2 (a modified version of Figure  1  in Brown et  al., 2006), mirror the dichotomy between inductive and deductive hypothesis testing (see Chaps. 2 and 3). Brown et al. (2006) conclude that using models to do experiments can lead to identification of key processes or phenomena within systems that may not be detectible in the more complex real world. As well, they suggest that coordination between models and field experiments can ultimately help realize comprehensive hypothesis testing. In a review of available tools for analysing human-landscape interactions, Zvoleff and An (2014) group models into four categories—statistical methods, GIS and spatial analysis methods, simulation approaches, and mixed methods. Although their review focuses specifically on models exploring how human activities affect landscapes, many of the strengths and weaknesses that they identify for each approach (reproduced in Table 10.1) can apply to landscape ecology research more broadly. Some applications of landscape ecology put more emphasis on quantitative modelling than others. For example, foresters have used silviculture models for decades, and so forest landscape ecologists have embraced modelling quite readily and combined these with various kinds of spatial and ecological models (Shifley et al., 2017). Scheller and Mladenoff (2007) reviewed forest landscape simulation models, all of which are spatially explicit, but vary in three key characteristics: whether they include spatial interactive processes (i.e., transfer of energy, matter, or information); whether they model static or dynamic communities and whether or

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Fig. 10.2  The relationships between pattern and process in landscape models. The left side of the figure shows how pattern data can be analyzed deductively to infer processes using descriptive/ statistical models), while the right side of the figure illustrates how process models can be built based on deductive hypotheses to predict pattern data (using mechanistic/mathematical models). (Adapted from Figure 1 in Brown et al. (2006) and reprinted with permission of the publisher, Taylor and Francis Ltd.)

not they include ecosystem processes. They identify 20 different forest landscape simulation models, and provide recommendations to readers on how to choose a model appropriate to a particular question. Despite the plethora of tools, and years of experience, modelling is not a panacea for understanding how forests function or will function in the future (Scheller, 2018), nor are all models suited for all questions (Verboom & Wamelink, 2005; Zvoleff & An, 2014). Table 10.2 summarizes some of the attributes of the models discussed in more detail in this chapter. When choosing an in silico approach, one needs not only consider what kind of question the model is addressing, but also whether the purpose of modelling is primarily to make predictions about future states (weather forecast models are a prime example of these), or to gain ecological insights on the mechanisms underlying the system (e.g., statistical inference). As well, some models are more realistic than others are; the degree of realism needed may depend in part on the question, but also on the way the model is applied. A model to inform decision-­ making may need to be more realistic than a model focused on understanding a system better. Finally, there are practical considerations of computing resources. Many of the types of landscape ecology experiments (with the possible exception of Types II.3 and II.4—in situ and ex situ experiments) described by Jenerette and Shen (2012) could be carried out in silico, with careful selection of the most appropriate tool. For example, tracer, translocation and transport experiments (Types I.2, II.5 and II.6 in Jenerette & Shen, 2012) could be conducted with agent-­ based models, while the experiments in group III (identification of process

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Table 10.1  General overview of some of the strengths and limitations of the four categories of modelling methods outlined by Zvoleff and An (2014). Table is reproduced with permission from Zvoleff and An (2014) Approach Statistical methods

Strengths Good for exploratory analysis Rapidly implemented Well-established methods for representing uncertainty

GIS and spatial Good for exploratory analysis analysis methods Excellent visualization tools

Simulation approaches

Can easily and precisely handle spatial data Can account for spatial autocorrelation Can integrate data from multiple temporal and spatial scales, can represent hierarchically structured systems and non-linear dynamics Integrate well with mixed methods

Weaknesses Difficult to examine system dynamics Common assumptions (e.g., normality, independence of residuals, linearity) are often not satisfied in landscape studies Some software packages stress visualization over analysis In can be too easy to make plots or maps with little theoretical support Support for temporal dimensions is traditionally weak in GIS tools Models can be difficult to construct, and are often hard to replicate

Understanding the structure of complex simulation models can be difficult even for experts Communication of uncertainty Good at representing interaction between system components, including sometimes overlooked feedbacks Mixed methods Good at representing qualitative Limitations and assumptions must be findings clearly communicated Wide range of techniques—Readers Good for decision-making under may be unfamiliar with individual uncertainty—Alternative policies can methods be explored Can consider long time horizons using qualitative storylines

sensitivity to landscape structure) could make use of cellular automata or system dynamic models. Pattern formation experiments (group IV) could exploit mathematical, statistical, or system dynamic models.

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Table 10.2  Comparison of attributes of model types discussed in this chapter

Model type Statistical

Mathematical/ mechanistic

Cellular automata Agent-based System dynamic

General purpose Test relationship between x and y variables on a landscape Test hypotheses about how different mechanisms/properties affect landscapes/ organisms Model landscape change as a function of different processes Model how organisms respond to landscape Model complex systems with ability to develop/test scenarios

Ability to gain ecological insights Some

Degree of Computing time required realism Low Low

Predictive ability High

Low

Low

High

Moderate to high

Depends on size of dataset High

High

Medium

Limited

Medium

Medium

Some

High

Low

High

Unknown

10.2  E  xamples of Different Types of In Silico Experiments for Landscape Ecology 10.2.1  Statistical Models Based on your experience of a typical undergraduate level course in statistics, you may believe that the purpose of statistics is to test whether your sample distribution matches a population distribution. You may not have thought of statistics as a type of model, and you more than likely have not considered them as a form of experiment. While fundamentally statistics is about comparing samples to populations, they are in silico models, in that the comparison between sample and population is a representation (i.e., a model) of the data-gathering process (Cox, 2006). This representation of data gathering is often highly idealized, imagining perfectly co-­ operative test subjects that are uniform in all ways but one and operating in an experimental arena free of confounding variables. Statistical models are also quantitative expressions of a hypothesis. If a research hypothesis explains why we think x is important to explaining some aspect of y, then the statistical hypothesis is the formal prediction of how a change in a specific direction of x will affect the direction of change in y. Thus, statistical models are an integral part of the experimental method. For example, Connors et al. (2013) hypothesized that landscape pattern in an urban environment would affect land surface temperature. Their statistical model linked spatial pattern (measured with class- and landscape-level metrics) to land surface temperature to determine which land use had the biggest effect. While their

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work represents an observational experiment, rather than a manipulative one, it illustrates the tight link between statistics and hypothesis testing. One of the most common types of statistical models in landscape ecology is species distribution models; indeed our discipline has produced several volumes dedicated to that topic (Franklin, 2010; Drew et al., 2011; Guisan et al., 2017; MacLeod, 2019). These models take georeferenced data on organisms’ location (‘occurrence data’) and sample various GIS layers that represent environmental, habitat, and resource variables for that species; what Austin (2002) calls the data model. The researcher integrates these data into a statistical model to assess whether and how the environmental variables exhibit statistically meaningful relationships to the species’ distribution (the ecological model, sensu Austin, 2002). From there, one can use the significant environmental covariates to extrapolate beyond the observed data to predict that species’ distribution over a larger spatial extent and/or in future points in time. The occurrence data may come from direct observations, or from proxy data, such as scat, track or hair samples, or via telemetry technology. Often, the statistical model is some kind of GLM, such as a binary logistic model, which requires both presence and absence data. This can introduce data challenges, since true absences are rarely recorded (Lobo et al., 2010), and confidently detecting a true absence can take a substantial amount of effort (for an example with a cryptic species and a very limited search area see Lauriault & Wiersma, 2019). Consequently, random data points may often substitute as ‘pseudo-absence’ data. There are various techniques to generate pseudo-absence data that are appropriate (for some examples see Barbet-Massin et al., 2012; Hanberry et al., 2012; Senay et al., 2013; Chapman et al., 2019). Alternatively, one can use models that only require presence (occurrence) data (see examples in Renner et  al., 2015; Grüss et  al., 2019; Liu et al., 2019). The details of how to carry out SDMs are not the focus here; the more important question in the context of this book is whether SDMs broadly are experiments or not. Many of the SDMs described in the literature (including some of the ones cited here) used machine-learning models. There is a fair bit of confusion about the difference between statistical and machine learning models (Bzdok et  al., 2018; Stewart, 2019); the most parsimonious (but not fully complete) way to distinguish the two is that machine learning emphasizes prediction, while statistical models emphasize trying to infer mechanisms between variables. However, the distinction is not very important. If we recall the criteria for an experiment from Chap. 2, one could argue that SDMs that seek to test hypotheses about which landscape features are most important for influencing species distributions are a form of experiment. Are they good experiments? Many of them make use of data on multiple observations of locations, and thus appear to have replication. However, one needs to be mindful of non-independence of data taken from multiple telemetry fixes on the same animal and ideally apply a mixed model approach using the individuals as random effects (see Chap. 4 for more detail). SDMs generally lack a strict treatment/control structure, and it is questionable whether the data are random. Very few SDMs carry out replicate analyses between landscapes, thus a model for species X in location Y is limited to that situation and does not allow for inference about that

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species more broadly across its wider distribution. Thus, SDMs may not be the most robust experiments. However, creative researchers have harnessed in silico techniques to experiment explicitly with simulated organisms and landscapes to test different properties of SDMs, including model performance, sample size effects, and methods to generate pseudo-absence. Such approaches (comprehensively reviewed by Meynard et al., 2019) are more explicitly experimental, and Meynard et al. (2019) provide guidelines for best practices for virtual simulations of SDMs. In a similar vein, papers that compare machine learning approaches (e.g., Liu et al., 2020) can be seen as in silico experiments focused on testing how different tools perform, rather than experiments on the landscape(s) or organism(s) featured.

10.2.2  Mathematical Models As described above, mathematical models are distinct from statistical models in that they explicitly try to model mechanisms using mathematical equations, rather than fit data to statistical models. For example, Borda-de-Água et al. (2011) use mathematical models to assess the impact of road networks on populations. They build on Skellam’s reaction-diffusion model to experimentally test four cases that manipulate characteristics of the population (e.g., dispersal ability, sensitivity to roads, carrying capacity, growth form), and the lethality of the roads. Three of the four cases are spatially explicit; in the remaining case, space is treated implicitly (Borda-de-­ Água et al., 2011). This is an example of a familiar landscape ecology question: how spatial arrangement of roads affects populations. A statistical model to assess this might have collected data on a species in landscapes with different road densities, or on different species within different landscapes, and tested how factors like road density or distance from roads affected species persistence or occurrence (see Rytwinski & Fahrig, 2007 for an example). However, by harnessing a mathematical model, Borda-de-Água et al. (2011) can experiment with whether different mechanisms might lead to the observed pattern(s) or not.

10.2.3  Cellular Automata Cellular automata (CA) models are models that are developed based on a regular grid of cells, each of which is assigned one of a finite number of states. The researcher develops rules that define whether and how cells change state at each time step in the model. The rules are often mathematical functions and can depend on the current state of the cell and/or the condition of a defined neighbourhood (a specified number of cells surrounding a focal cell). Cellular automata models are often used in planning (Silva et al., 2008) and in future landscape modelling (e.g., Bosch & Chenal, 2019; Pickard & Meentemeyer, 2019). Examples of CA models that are particularly germane to landscape ecology are LANDIS (Scheller &

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Mladenoff, 2004) and LANDIS-II (Scheller et al., 2007). Researchers around the world have used LANDIS and LANDIS-II to simulate forest landscape change over scales of time from decades to centuries and over spatial extents of millions of hectares (see list of publications on the LANDIS-II website, which you can find in the Resources section of the book). Another example of a CA model is the WoodPaM model; a spatially explicit simulation of wood-pasture ecosystem dynamics that was developed by Gillet (2008) and further refined by Peringer et al. (2013). This model captures the dynamics of silvopastoral ecosystems, a common ecosystem type in central Europe. The model uses differential and algebraic equations to model seedling development, and includes sub-models for the landscape mosaic, the herbaceous plants, woody plants and cattle. Peringer et  al. (2016) used this tool to test how low-intensity grazing affected vegetation dynamics. They noted that, while experimental field studies had yielded some insights, these usually had a limited time span and spatial extent. Thus, the model would allow them to test the relative contributions of cattle herbivory and plant traits to landscape pattern over longer periods of time (they projected forward 1500 years in 100-year time steps) and across landscapes that are more expansive. Peringer et al. (2016) based their simulations on two real world pastures that functioned as model systems; their work showed that increases in tree dispersal ability and increases in resistance to browsing led to increases in forest cover, while enhanced grazing pressure did not change the landscape pattern significantly from the baseline. CA models such as the WoodPaM and LANDIS/LANDIS II tools can use a rule-­ based approach to project how a landscape might change over time. This is an example of “future landscape modelling”, which is a type of research that couples landscape ecology with social scientific research in psychology, policy and socioeconomics. Meentemeyer et  al. (2013) developed a future landscape simulator focused on urban geographies called FUTURES (FUTure Urban-Regional Environment Simulator). This simulator forecasts landscape change as a function of three sub-models of land change drivers (demand, site suitability and spatial structure). The changes are simulated based on an algorithm that takes cell-level transitions from one state (e.g., forest) to another (e.g., farmland) while taking into account spatial structure to make growth of different patches realistic and following historical patterns of development. FUTURES was initially calibrated to the Charlotte, North Carolina metropolitan region (Meentemeyer et al., 2013), but has since been applied to other regions of the world including cities in Asia (Lei et al., 2020; Jayasinghe et al., 2021; Liang et al., 2021; Shi et  al., 2021) and Europe (Cosentino et  al., 2018). FUTURES has also been used to infer how current drivers might shape future urban growth (e.g., Liang et  al., 2021) and model trade-offs that different planning decisions may create (Shoemaker et al., 2019; Schwaab et al., 2020). This latter application illustrates the experimental nature of in silico approaches well. Meentemeyer et al. (2013) wanted to test how urban design affected ecosystem services under different planning decisions. They treated different planning scenarios (“business-as-usual”, sprawl, and infill) as hypotheses to test how well the future landscape of Charlotte would

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provide ecosystem services of water purification, carbon storage, and vertebrate habitat. It would be impossible to do a manipulative experiment on the city of Charlotte that tested all three scenarios, and an experiment that allocated different planning treatments to different cities would be confounded by inherent physical, biological and socio-economic differences between the cities. Thus, the only way to experiment in this kind of research is through an in silico model. As with forest management, where the results of planning decisions may not be evident for decades, urban and landscape planning is a topic especially amenable to in silico experimentation. Although movement models are often agent-based models (see below), cellular automata models have also been harnessed to model the spread of species under different landscape configurations (Crespo-Pérez et al., 2011; Coulon et al., 2015). In a study in a remote part of the Andes in Ecuador, Crespo-Pérez et al. (2011) used road work as a natural experiment to study spatial spread of an invasive potato tuber moth (Tecia solanivora). They harnessed a cellular automata model of 1600 grid cells that represented environmental data for the real region, which was 20 km × 20 km in size. They used this model to test how much environmental context vs. human activities affected spread of the moth. They specifically wanted to investigate how the spatial distribution of crop storage structures modified the local microclimate to influence the presence of this pest, and how the movement of the moth was facilitated by human transportation. Actively manipulating human movement in a region this size would not be a feasible experiment and experimentally manipulating placement of storage structures would be costly. The researchers inoculated the model with 90 moths, located in the simulated location of the village that was the main source of the infestation in the real world (Crespo-Pérez et al., 2011). At each time step (representing one generation in the life history of the moth), they used a stage-structured model to describe the population dynamics of the moth in each cell. This is an example of how mathematical models (in this case demographic models for survival, dispersal and reproduction as a function of density and/or microclimate) inform the algorithms within a CA model. The experimental treatment consisted of model runs with different densities of storage silos, with known effects on microclimate, which in turn would affect reproduction and survival. The researchers developed a probability model for the effect of moths moving from an infected area to a non-infected area by hitchhiking with human travel; this model used the distance traveled and the size of the source village as predictor variables. The experimental treatment consisted of model runs with different simulated propagule sizes that travelled. Because the potato tuber moth was travelling through this region in real time, the researchers were able to use survey data and participatory monitoring by farmers to validate their model with field data. This allowed them to determine that controlling the microclimate within storage structures would be the most effective strategy to minimize the insect’s spread (Crespo-Pérez et al., 2011).

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10.2.4  Agent-Based Models Agent-based models are those that simulate how an autonomous “agent” (individual organisms, for example, but also larger entities such as herds) behave in response to landscape attributes. As stated above, researchers often use agent-based models to experimentally test questions about animal movement. For example, Coulon et al. (2015) simulated animal movement of two species—a bird and an amphibian—to better assess how their predicted movement in a fragmented landscape matched known genetic connectivity. They compared measures of landscape connectivity obtained via their agent-based model (they called it a “stochastic movement simulator” or SMS) with measures of connectivity patterns (simple Euclidean distance measures, and more complex connectivity metrics based on least-cost paths and circuit theory). The researchers use least-cost surface raster values for their simulated amphibian that were based on results from the micro-landscape experiment for natterjack toads (Epidalea calamita, discussed in more detail in the next chapter), and set movement parameters (perceptual range, directional persistence, memory size and number of steps) based on literature. They used their model to experimentally simulate dispersal bias and directional persistence (Coulon et al., 2015). They found that their SMS modeled connectivity better then any of the pattern-based approaches. However, they caution that individual-based models have limitations and caveats. They can be “data hungry” or there may not be sufficient data for proper parameterization. Agent-based models are not limited to mobile organisms. Braziunas et al. (2018) applied an individual-based model, iLand, to four species of conifers in Yellowstone National Park, to simulate stand development based on models of individual trees that were greater than 4 m in height, at a one-hectare resolution. Their experiment focused on testing whether abiotic conditions vs. regeneration densities affected post-fire stand development over a 300-year time horizon. The experiment used a 2 × 2 factorial simulation to test these two drivers, each at two levels—the observed variation of each factor (abiotic conditions and regeneration density) in post-fire or without any variation. Obviously, without a time machine to travel 300 years into the future, they are unable to validate the 300-year projections. However, their model projections did realistically match the structures of current 300-year old stands in the region. The authors’ approach suggested that variation in initial post-­ fire regeneration density was the most important driver of stand trajectories (Braziunas et al., 2018). Agent-based models are also useful to test questions about habitat preference. For example, Byers et al. (2018) hypothesized that host habitat preference results from the ways in which dispersing individuals respond when they reach habitat boundaries. They modelled movement of individual simulated insects, with in silico manipulations of movement rules, to test whether any of their three hypothesized behaviours resulted in equilibrium populations of their simulated organisms that matched observed insect responses to optimal habitat (in their case, date moth Batrachedra amydraula fidelity to plantations surrounded by deserts). Their

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simulations showed that the number of individuals in host habitat at equilibrium depended on rebounding probability at the boundary, coupled with the ratio of the host habitat to the larger area. When they used simulated data to estimate catch rates of moths within and outside a date plantation, their observed catches and calculations of habitat preference matched the simulations very closely. Because direct observations of movement of such insects is not feasible, and even densities can only be estimated from trapping, in silico simulations here provide a platform to experiment with how different movement behaviours affect densities. Behavioural responses to habitat can also be modelled in response to patch pattern; Nams (2014) tested whether the probability of crossing from one patch into another was affected by the tortuosity of the edge between the patches, and if this changed depending on the degree to which the simulated organism was attracted to edges. Nams (2014) points out that many animals likely respond with different behaviours to edge shape, but that only a few studies have tested this. This is not surprising, as it would be labour intensive to study in a micro-landscape (see Chap. 11), and would require high precision telemetry to study in a large-scale field experiment, such as the ones described in Chap. 6. Thus, an in silico model to test is a logical approach and Nams (2014) showed that edge tortuosity affected how permeable an edge was, but that this did not apply to animals that were attracted to edges and was sensitive to scale issues for those organisms that avoided, or were neutral to, edges. However, to be maximally useful, such a model should be validated with real-world data—as the Byers et al. (2018) date moth model was. In a further example of in silico assessment of the effects of landscape pattern, but this time applied to populations instead of individuals, Dalkvist et  al. (2013) used an agent-based model to test three different hypotheses about population persistence for voles (Microtus agrestis) in unmanaged grasslands adjacent to orchards that experience annual pesticide treatments. Their in silico experiment modelled individual vole probabilities of transitions from one life stage to another along with probabilities of moving through the landscape. By aggregating modelled individuals to the population level, they could experimentally test if different landscape configurations affected vole population persistence. The modelled landscape configurations (which included four different levels of grassland cover across the landscape, two different levels of orchard cover, and variation in the spatial arrangement) would not be possible to manipulate experimentally in a single landscape. Dalkvist et al. (2013) showed that the pesticide application in the orchards (aimed at treating non-vole pests) reduced the vole populations, but that there was less impact in landscapes with a high proportion of grassland habitat, and in those with less distance between grasslands and orchards. Another approach to understanding population-­ level responses from individuals is to combine agent-based models with equation-­ based ones, as Marilleau et  al. (2018) did for the same species, with the goal to assess which combination of simulation parameters matched observed population patterns, including spatial spread. Response variables in agent-based models need not be abundance or population size; Hovel and Regan (2008) modelled predator-prey behaviour as a function of different degrees of habitat fragmentation in an in silico model of a three-trophic

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food chain in seagrass habitat. They created four simulated landscapes: a continuous habitat as the control, and three levels of fragmentation. On these simulated landscapes, they distributed prey (juvenile blue crabs, Callinectes sapidus), mesopredators (adult blue crabs) and predators (large fishes) using a random distribution or one of three settlement patterns. The agents were assigned three types of movement (random, predation avoidance and directed hunting), which differed in their parameters depending on the agent’s location within the interior of the habitat patches, the edge, or the matrix (Hovel & Regan, 2008). The experiment tested how habitat fragmentation affected predator and prey behaviour and final crab survival across the four landscapes and with different movement scenarios. Hovel and Regan's (2008) overall finding suggested that prey population dynamics did not differ significantly between different levels of fragmentation within the simulated landscapes, except when prey movement was highly restricted or when predators hunted randomly. As we saw in Chaps. 6 and 7, actively manipulating habitat fragments and assessing individual movements is challenging to do in the real world. This experiment echoes some of the Bowling Green work that looked at arthropod movement in response to fragmentation—but examining trophic interactions adds another layer of complexity that would be more labour intensive in the real world. Hovel and Regan (2008) describe past manipulative experiments that restricted prey movement by tethering prey (see the description of a similar experiment on pinfish in the Tampa Bay experiment in the next chapter), and assessed how predation varied based on whether tethered prey were in large or small fragments. However, there have been critiques that tethering itself presents a treatment level bias, and so an in silico experiment that models the effect of tethering (i.e., highly limited movement) along with intermediate levels of movement, might be more realistic. As seen in other examples in this chapter, in silico models that match real-world experiments or observations can help offer insights into some of the driving mechanisms. In this case, Hovel and Regan (2008) concluded that their model matched field experiments with tethered crabs, but that tethering experiments also biased the relative differences in mortality estimates across fragment sizes. Thus, in silico approaches are not only able to do things that are difficult or impossible in the real world, they can also help untangle biases in real-world experiments. As illustrated in the above examples, agent-based models can vary in their complexity. Pauli et al. (2013) argue that too many models over-simplify animal behaviour and render these models less valuable. At the same time, they acknowledge that overly complex models can be computationally intensive. However, they make two arguments: (1) model users should be able to control the degree of complexity in the models; (2) that a sufficient amount of complexity allows for investigation into questions that would be difficult to address in manipulative field experiments (Pauli et  al., 2013). Their paper describes the SEARCH (Spatially Explicit Animal Response to Composition of Habitat) model, which simulates animal dispersal across a GIS landscape. In contrast to the agent-based movement models above, the GIS landscape in SEARCH is vector-based, and not raster based. Those readers considering using in silico models as an experimental approach should pay attention to the ODD (Overview-Design Concepts—Details) protocol they employ to describe

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their model (Pauli et al., 2013). Researchers have since applied the SEARCH model to understand the continuum of behaviour of Burmese pythons Python bivittatus (Mutascio et  al., 2017), how flying squirrels Glaucomys sabrinus griseifrons respond to habitat connectivity (Trapp et al., 2019) and to model translocated martens Martes americana to understand plasticity in dispersal behaviour (Day et al., 2019).

10.2.5  System Dynamic Models System dynamics (SD) models are highly abstract models that ignore fine details to provide a general representation of complex systems. Originally developed for use in the corporate world, these models have recently been applied to environmental and ecological concepts such as water management (Leitman et al., 2016; Zhang et al., 2021) and impacts of overgrazing (Ibáñez et al., 2007). SD models are useful for large-scale problems that have non-linear and dynamic changes, with multiple parameters and feedbacks. In landscape studies, system dynamic models have been applied to issues of urban sprawl (Lee & Choe, 2012; Li et al., 2021; Xu et al., 2015) and land-use (Mao et al., 2014). SD models can capture the complexities of urban landscapes using subsystem models—for example, Xu et  al. (2015) developed industry, environment, economic, population and landscape ecology subsystems to model industrial growth and impacts on landscape ecology in China. SD models can be superior to CA models for predicting processes such as urban growth, because they can capture the complexities of social, economic and environmental factors that extend beyond the neighbourhood cells (Lee & Choe, 2012). SD models can be appealing when interacting with decision makers, because the underlying mathematical/computational model is often visualized using a readily interpretable map or flow diagram of the interactions. Many SDs include interactive GUI interfaces that allow a user to manipulate elements of the model and assess the impact visually. Researchers are only just beginning to use SD models in landscape ecology, so far only within urban landscapes. It will be interesting to see if others working in other types of landscapes apply SD models to solve complex problems.

10.2.6  Combined Models In some cases, it is profitable for researchers to combine different models and in silico approaches to address a research question. This need not be complex. In some cases, researchers have integrated models originally developed for different applications and harnessed them to address landscape ecology questions. For example, Gaucherel et al. (2010) developed an integrated assessment of bioenergy production at landscape scales to assess how areas devoted to biomass production might be distributed in a landscape, and what the aesthetic implications of this might be. The

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models consisted of two models that the team had previously developed: a human-­ driven agricultural model (called DYPAL—Dynamic Patchy Landscape) and a climate-­driven forest model (called MAIDEN). Their motivation was to test whether land allocation scenarios that yielded the greatest economic benefit also had the highest biomass. The experimental aspect of this project tests scenarios under random crop and grassland rotations, vs. land change forecasts based on plausible scenarios. In some cases, researchers will use both mathematical and statistical models in a complementary fashion. Numminen and Laine (2020) used this approach to model the spatial spread of a wild plant pathogen, and to test how road networks affected pathogen spread. Numminen and Laine combined a discrete time-step model with a Generalized Additive Model (GAM). The discrete time-step model calculated pathogen infection probability for the host plant population, based on a calculated rate of infection that included terms for relative transmission along roads and along land, as well as distance between plant populations. The GAM then fit pathogen presence-absence through time to determine the effect of road network and distance between plant populations. The experimental part of the study comes when they model three different scenarios: (1) same transmission distance for the pathogen; (2) different transmission distances and rates along roads and across land; and (3) same transmission rate along road/land (Numminen & Laine, 2020). The statistical model enabled the researchers to investigate whether physically distanced populations were functionally connected via road networks. The mathematical model only captured short distances and did not account for variations in traffic levels along roads. Though dense, this paper is a nice example of the complementarity of mathematical and statistical approaches, as well as the need for large data sets—their study had infection data from over 3400 plant populations. Work that examines processes in space and time—such as forest insect disturbances—also makes use of multiple model types. Perez and Dragicevic (2012) combined swarm intelligence (SI) and agent-based models to represent fine-scale insect response to forest disturbance at the level of individual trees. Cellular automata modelling with GIS simulates tree mortality due to insect infestation as a consequence of different larger-scale drivers (e.g., wind direction), and thus links fine-scale and broad-scale processes (Perez & Dragicevic, 2012). Their currently modelled landscape is a hypothetical one. However, it is possible to envision experimental in silico manipulations of landscape pattern (for example, having larger gaps between forest patches that are oriented in the direction of the prevailing winds) to see whether certain land management scenarios might minimize insect outbreaks. This could help inform adaptive management scenarios—whereby management strategies are applied experimentally. Because some management is expensive (and potentially irreversible), models provide a way to do a preliminary assessment of probable outcomes. In silico approaches can integrate optimisation algorithms with both statistical and simulation models to identify the spatial arrangement of crop cover types to minimize pest impacts (Parisey et al., 2016). Integrating models with adaptive management need not involve complex, multi-part models either. For example, Peck (2014) suggests that agent-based models allow managers to explore

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options and the potential outcomes before actively applying management actions to a particular issue. Indeed, as part of an adaptive management strategy, the agent-­ based model of vole populations in response to pesticide treatments (Dalkvist et al., 2013) could be used to determine a reasonable range of pesticide application strategies before actually carrying out any spraying in the real world. Schuwirth et al. (2019) provide guidelines for integrating modelling into management that would be valuable for anyone developing a model within an applied management context.

10.3  Advantages and Disadvantages of In Silico Experiments It should be clear by now that in silico experiments have a great deal of potential to carry out studies that would be challenging or infeasible in the real world. As Box’s aphorism “all models are wrong, but some are useful” implies, some consideration of their limitations is necessary. In all modelling work, the “garbage-in-garbage-­ out” motto also applies. Thus models should be parameterized with appropriate data, and should be validated with data from the system they are modelling, either through concurrent or post hoc data collection (e.g., Jonsen et al., 2007; Pickard & Meentemeyer, 2019). For futures modelling, back-casting (e.g., Meentemeyer et al., 2013) is a critical step, with the assumption that a model that predicts the past well is more likely to make reasonable predictions about the future. In some temporal models, a “burn-in” period is critical, before actively manipulating the system to experiment with the effect of different parameters or scenarios on the feature of interest. For example, in the vole-orchard model, Dalkvist et al. (2013) had a 20 year burn-in period, while in the WoodPaM model, Peringer et al. (2016) first ran the model to simulate 500 years to allow the landscape to reach a closed forest “climax” state, before they simulated pasture impacts. When using in silico models for landscape ecology, scale and complexity are key considerations. Bonnell et al. (2016) showed that model outcomes are sensitive to spatial and temporal scales. Thus, anyone embarking on an in silico experiment should consider whether the scale of data available to the model is appropriate to the question. In some cases, the problem may be one of reconciling fine-scale patterns with larger-scale outcomes, as we saw above with the forest insect modelling work (Perez & Dragicevic, 2012), or the vole models that combined individual- and population level processes (Marilleau et al., 2018). For further reading, Moreira et al. (2009) provide a framework for integrating models to allow for multi-scale models that link bottom-up and top-down processes. Indeed, the tensions between the complexities of the real-world, and the utility of models to address them is at the crux of the imagined dialog in Seppelt et al. (2009). Landscape ecologists who come to the discipline from either the life sciences or earth sciences may have had limited training in computing and quantitative methods (Barraquand et al., 2014). For them, making the leap into experiments like the ones described in this chapter may be daunting, and they may feel as overwhelmed as “Tony” in the fictional encounter described in Seppelt et al. (2009). It does not have

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to be scary! Remember that we are an interdisciplinary discipline. You can find a landscape ecologist who came to the discipline from a quantitative background to collaborate with, and from whom you can learn. Much of the culture around quantitative modelling now emphasizes open-source software and data. This culture comes with clear guidelines for researchers to meet standards of reproducibility and transparency, that are intended to make it easy for others to use (Hampton et al., 2015; Hart et al., 2016). Data repositories like Zenodo, FigShare and Dryad, and sources like GitHub are resources that were not around when I was a graduate student and are worth making use of (see the “Resources” section of this book for more details). The increased use of the open-source programming language R across ecology (Lai et al., 2019) means there are packages tailored to ecological problems (for a recent paper that provides a guide to R packages particularly useful for landscape ecology see Hesselbarth et al., 2021), along with online support. Some of the papers cited here (e.g., Dalkvist et al., 2013) include full online documentation of the code as well as links to the open-source platform that they used to develop the model. Others follow the ODD protocol (Pauli et al., 2013; Bonnell et al., 2016; Marilleau et  al., 2018) to their model description, which can facilitate your understanding. Depending on the complexity of the model, computing power can be an issue. Some of the models summarized here took time to run (although one should be mindful of the year of publication, and the fact that computer storage and speed are much more affordable than they were even a decade ago). For example, the vole-­ orchard models took a number of hours per replicate (Dalkvist et al., 2013), and the stochastic movement simulator used to model movement of amphibians and birds (Coulon et al., 2015) took 18 h to run on a standard laptop for the day. Many universities have access to distributed computing networks, which can help to address these limitations. The increased availability of cloud computing platforms (see the “Resources” section for a guide) facilitate access to memory and CPU without needing to buy an expensive mainframe. If you find yourself developing a model that is using up all of your computer’s power, I suggest you seek out your campus’ computer science department or your agency’s IT resources for advice; it is very likely that they can help you find better resources. The first generation of landscape ecologists in North America were the ones who may have used mainframe computers as graduate students. My generation went through graduate school with a personal computer on their desk, but limited storage and speed and no Web 2.0. The current generation of landscape ecology graduate students has grown up not knowing a world without mobile computing, and widespread sharing of data and information across the web. Thus, there are likely experimental possibilities in the future that we cannot yet imagine. As with all of the experimental approaches described in this book, in silico experiments work best when carried out in parallel with other approaches. The fictional modeller Rebecca, in Seppelt et  al. (2009), concludes that the “virtual landscape lab” offers several connections to the real world worth exploring. We can harness in silico experiments to study virtual landscapes in a virtual lab. We can test our theories in silico with real-world data. We can develop scenarios to facilitate meaningful interaction with

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stakeholders and decision makers. Models can help us identify efficient methods for sampling and monitoring in the real world (Seppelt et  al., 2009). By not fearing computers, we can realize these opportunities.

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Parisey, N., Bourhis, Y., Roques, L., et  al. (2016). Rearranging agricultural landscapes towards habitat quality optimisation: In silico application to pest regulation. Ecological Complexity, 28, 113–122. https://doi.org/10.1016/j.ecocom.2016.07.003 Pauli, B.  P., McCann, N.  P., Zollner, P.  A., et  al. (2013). SEARCH: Spatially explicit animal response to composition of habitat. PLoS One, 8, e64656. https://doi.org/10.1371/journal. pone.0064656 Peck, S. L. (2014). Perspectives on why digital ecologies matter: Combining population genetics and ecologically informed agent-based models with GIS for managing dipteran livestock pests. Acta Tropica, 138, 22–25. https://doi.org/10.1016/j.actatropica.2014.03.006 Pelletier, D., Claudet, J., Ferraris, J., et al. (2008). Models and indicators for assessing conservation and fisheries-related effects of marine protected areas. Canadian Journal of Fisheries and Aquatic Sciences, 65, 765–769. https://doi.org/10.1139/F08-­026 Perez, L., & Dragicevic, S. (2012). Landscape-level simulation of forest insect disturbance: Coupling swarm intelligent agents with GIS-based cellular automata model. Ecological Modelling, 231, 53–64. https://doi.org/10.1016/j.ecolmodel.2012.01.020 Peringer, A., Siehoff, S., Chételat, J., et al. (2013). Past and future landscape dynamics in pasture-­ woodlands of the Swiss Jura Mountains under climate change. Ecology and Society, 18, 11. https://doi.org/10.5751/ES-­05600-­180311 Peringer, A., Schulze, K. A., Stupariu, I., et al. (2016). Multi-scale feedbacks between tree regeneration traits and herbivore behavior explain the structure of pasture-woodland mosaics. Landscape Ecology, 31, 913–927. https://doi.org/10.1007/s10980-­015-­0308-­z Pickard, B. R., & Meentemeyer, R. K. (2019). Validating land change models based on configuration disagreement. Computers, Environment and Urban Systems, 77, 101366. https://doi. org/10.1016/j.compenvurbsys.2019.101366 Renner, I. W., Elith, J., Baddeley, A., et al. (2015). Point process models for presence-only analysis. Methods in Ecology and Evolution, 6, 366–379. https://doi.org/10.1111/2041-­210X.12352 Rytwinski, T., & Fahrig, L. (2007). Effect of road density on abundance of white-footed mice. Landscape Ecology, 22, 1501–1512. Saltelli, A. (2019). A short comment on statistical versus mathematical modelling. Nature Communications, 10, 8–10. https://doi.org/10.1038/s41467-­019-­11865-­8 Saltelli, A., Bammer, G., Bruno, I., et al. (2020). Five ways to ensure that models serve society: A manifesto. Nature, 582, 482–484. https://doi.org/10.1038/d41586-­020-­01812-­9 Scheller, R.  M. (2018). The challenges of forest modeling given climate change. Landscape Ecology, 33, 1481–1488. https://doi.org/10.1007/s10980-­018-­0689-­x Scheller, R. M., & Mladenoff, D. J. (2004). A forest growth and biomass module for a landscape simulation model, LANDIS: Design, validation, and application. Ecological Modelling, 180, 211–229. https://doi.org/10.1016/j.ecolmodel.2004.01.022 Scheller, R.  M., & Mladenoff, D.  J. (2007). An ecological classification of forest landscape simulation models: Tools and strategies for understanding broad-scale forested ecosystems. Landscape Ecology, 22, 491–505. https://doi.org/10.1007/s10980-­006-­9048-­4 Scheller, R. M., Domingo, J. B., Sturtevant, B. R., et al. (2007). Design, development, and application of LANDIS-II, a spatial landscape simulation model with flexible temporal and spatial resolution. Ecological Modelling, 201, 409–419. https://doi.org/10.1016/j.ecolmodel.2006.10.009 Schuwirth, N., Borgwardt, F., Domisch, S., et al. (2019). How to make ecological models useful for environmental management. Ecological Modelling, 411, 108784. https://doi.org/10.1016/j. ecolmodel.2019.108784 Schwaab, J., Lautenbach, S., Braun-Dubler, N., et al. (2020). The difficulty of steering settlement development to reduce the loss of ecosystem services: An exploration of different development scenarios in Switzerland using spatially explicit land-use models. Journal of Environmental Planning and Management, 63, 1037–1055. https://doi.org/10.1080/09640568.2019.1631762 Senay, S.  D., Worner, S.  P., & Ikeda, T. (2013). Novel three-step pseudo-absence selection technique for improved species distribution modelling. PLoS One, 8, e71218. https://doi. org/10.1371/journal.pone.0071218

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Chapter 11

Novel Landscapes

Oh brave new world! Shakespeare, The Tempest

11.1  Introduction The chapters in this book up to this point have introduced different approaches to doing experiments in landscape ecology. In Chaps. 6 and 7, I discussed large-scale manipulative experiments in terrestrial landscapes on the scale of tens to thousands of hectares (Chap. 6) and on experimental model landscapes of a few hectares (Chap. 7). In Chaps. 8 and 9, I discussed how container experiments that were either artificial (mesocosms; Chap. 8) or naturally bounded (microcosms; Chap. 9) could be harnessed for a suite of different experiments. In Chap. 10, I presented how in silico experiments (computer models) are a yet another kind of experimental arena. In this chapter, I am asking landscape ecologists to “think outside the box” a little bit, and consider novel landscapes that might be amenable to experimental work. In some cases, these novel landscapes may allow for different kinds of experiments than the systems discussed to this point, or may have advantages over some of these more “typical” terrestrial landscape systems. Three of these “novel” landscapes—seascapes, riverscapes, and soundscapes— may not sound that radical or different to many landscape ecologists. After all, a book on seascape ecology (Pittman, 2018) has been reviewed in our flagship journal (Kavanaugh, 2019), and there is a volume on soundscape ecology (Farina, 2014) aimed at landscape ecologists. Prominent landscape ecologists have written about developing linkages between terrestrial landscapes and riverscapes (Wiens, 2002). However, the nature of experimentation in these three types of landscapes is a little different from the terrestrial landscapes that tend to dominate most work in landscape ecology. A further type of novel landscape, “microlandscapes”, may seem at first glance to simply be another word describing the environments used in the meso/microcosm © Springer Nature Switzerland AG 2022 Y. F. Wiersma, Experimental Landscape Ecology, Landscape Series 29, https://doi.org/10.1007/978-3-030-95189-4_11

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experiments already discussed in Chaps. 8 and 9. While these certainly share similarities to mesocosms and microcosms (and indeed, Larsen and Hargreaves (2020) refer to microlandscapes as either micro- or mesocosms), microlandscapes are a unique type of landscape in that they are artificially constructed landscapes—usually in a lab setting—which mimic aspects of real world landscapes. Finally, I offer up some unusual “landscapes” for consideration, specifically corporeal and histological ones. In all of these landscapes, the novelty of the system warrants some considerations for experimental design that are uniquely different from what we have discussed in previous chapters.

11.2  Experiments in Seascapes The word “seascape” first appeared in the journal Landscape Ecology in a 1989 paper (Steele, 1989), although a few papers made use of the term in the broader literature before that date (see Fig. 1 in Bell & Furman, 2017). In a chapter of a book dedicated to the topic of seascape ecology (Pittman, 2018), three prominent American landscape ecologists (John Wiens, Jiango Wu, and Dean Urban), all of whom had been involved in the development of the discipline, provided some opinions on the emerging field (Pittman et al., 2018). In it, John Wiens described his “aha” moment, when he realized while at sea that his previous conception of the ocean as a homogenous wet mass was incorrect (Fig. 11.1). He observed that foraging aggregations were analogous to patches in the terrestrial landscape, and that the seascape has structure, function and dynamics, all of which operate across scales of space and time. He noted that applying landscape ecology concepts and tools to the benthic environment might be relatively straightforward, but could prove a challenge in the pelagic ocean. The different physical and chemical natures of water masses led Manderson (2016) to opine that seascapes were not landscapes, and that the unique constraints that living in a liquid medium put on organisms meant that the paradigms of landscape ecology would not apply. In a commentary on Manderson’s “food for thought” essay, Bell and Furman (2017) pointed out that benthic systems carried all the characteristics of terrestrial landscapes in terms of patch dynamics, and supported the need to distinguish coastal, benthic and pelagic environments in terms of delineating seascapes. Manderson (2017) countered with an argument that the liquid nature of the medium in which pelagic organisms operated meant that they were fundamentally different from terrestrial environments, and thus applying rules from terrestrial landscapes to seascapes would be problematic. In the chapter in Pittman et al. (2018) mentioned above, Jianguo Wu responded to Bell and Furman's (2017) critique by positing that this divergence in the characteristics of coastal vs. pelagic seascape simply meant that the relevance of particular landscape ecology concepts varied across different ocean environments (i.e., coastal, benthic, pelagic). Wu, in Pittman et  al. (2018), contended that the open ocean still had many of the

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Fig. 11.1  A schematic 3D cube of a seascape, illustrating structural pattern, including patches and gradients. Image created by Simon J. Pittman. Used under CC BY-SA 4.0 License

characteristics of terrestrial landscapes, including patch structure, dynamics, gradients, and scale. In a pithy statement, Dean Urban proposed that seascapes “might be seen as particularly fast-moving versions of landscapes” (Pittman et al., 2018, p. 492). The view of the majority of landscape ecologists who have grappled with the seascape/ landscape question appears to be that seascapes are landscapes and that many of the same concepts and questions that we explore in terrestrial landscapes can apply here. However, life in the sea is different from life on land. We can adopt some of the techniques we use on land for use in the marine realm, but we will need to develop others to work in the unique conditions of the sea. The emphasis of 3-­dimensional movement of organisms and materials in the ocean environment is one feature that distinguishes seascape studies from most terrestrial landscape studies. Given this, what can we learn from experiments in this unique environment? Can some of the lessons from conducting experiments in this unique environment help us with experimentation in landscape ecology more broadly? Let us start with experiments in the benthic environment. Although the benthos might be viewed as analogous to the terrestrial landscape (after all, it has landforms, land cover and land uses; three of the hallmarks of landscapes sensu Turner (1989)), but simply one covered by water instead of air; conducting research in the benthos, particularly the deep benthos, carries challenges. Indeed, my marine ecologist colleague Paul Snelgrove once told me that doing benthic sampling on the high seas was the equivalent of a terrestrial ecologist doing quadrat sampling from a hot air

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balloon on a dark, windy night! Underwater autonomous vehicles and remote video imaging may be changing that somewhat, but the point is that a researcher cannot interact directly with the deep ocean environment. Most benthic research in the deep ocean consists of observational experiments, but in the shallow benthos, accessible by SCUBA divers and snorkelers, manipulative experiments are possible. Indeed, we have already seen an example of a shallow-water experiment in Chap. 9 with Munguia's (2007) use of dead pen shells (Atrina rigida) as microcosms to examine aggregations of fauna. In an experiment that could be labelled a “mesocosm without walls”, Chacin and Stallings (2016) tethered pinfish (Lagodon rhomboids) to 0.5 m × 0.5 m patches of artificial seagrass that varied in shoot density (3 levels; none, medium and high) and that were placed in two areas of Tampa Bay that varied in their turbidity. This allowed them to test how the interaction between predator visibility (the two turbidity levels) and the density of grass in which to hide in affected pinfish predation. Although in many ways this pinfish study is a classic behavioural ecology experiment, behavioural ecology studies that look at responses to the environment, and do so where there is an explicit spatial dimension to the environmental conditions, overlap conceptually with landscape ecology. Chacin and Stallings' (2016) experiment is similar to some of the mesocosm experiments we saw in Chap. 8 that manipulated patch quality. For example, the backswimmer (Notonecta undulata) experiments that manipulated habitat quality in the tanks (Baines & McCauley, 2018) or the experiments that added nutrients (Masese et al., 2020) or dyes (Suski et al., 2018) to aquatic mesocosms to see effects on the ecosystem, all manipulate patch quality in one way or another. Because the benthic environment shares similar patch-mosaic structure with the terrestrial environment, we see parallels in concepts and methods. For example, in a review of reef fish movement, Appeldoorn et  al. (2009) borrowed a theoretical framework from terrestrial landscape ecology (Wiens, 1992), which predicted that movement between patches was a function of the contrast between habitat patches. Citing several studies that tracked fish movement between reef patches (examples of experiment Type I.2 in Jenerette & Shen, 2012), they concluded that Wiens' (1992) framework of thinking about movement in terms of patch contrast did explain many of the observed patterns of fish movement (Appeldoorn et al., 2009). However, they noted that a second theoretical framework, that took into account ontogenetic shifts in behaviour of fish to trade-off predation risk and foraging opportunities (Werner & Gilliam, 1984), also explained some of the movement behaviour, and that further work was necessary to merge these two frameworks (Appeldoorn et  al., 2009). Another example of terrestrial concepts migrating to seascapes is a project investigating how spatial mosaics create refugia for less competitive species during early succession in an underwater boulder field in Australia (Liversage, 2020). The paper directly cites earlier terrestrial landscape ecology concepts of spatial mosaics and scale issues (Wiens & Milne, 1989). The patch structure of the benthic environment also results in similar experimental tools. For example, in an experiment to test whether grazing affected the density of macroalgae on artificial substrates (e.g., jetties, pilings), Ferrario et  al. (2016) used cages of two mesh sizes to exclude two different types of grazers. Similarly, to

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assess how seascape structure affected intertidal food webs in New Zealand, Rilov and Schiel (2006) created cages that excluded predators to assess how predation pressure influences mussel species patterns. They also tested for seascape context by deploying their experiments in areas with and without subtidal reefs, and found that the seascape context played an important role in structuring the food web in addition to top-down predation (Rilov & Schiel, 2006). These exclosure experiments are similar, but on a much different scale, to the large-scale manipulation on Australian cattle farms that used fences to exclude sheep, that we saw in Chap. 6 (Kay et al., 2017). Other experiments in benthic seascapes that mirror those in the terrestrial landscape are those that manipulate internal patch quality (Type III.7  in Jenerette & Shen, 2012), for example, by introducing a disturbance. In the Australian study to test for refugia in boulder field seascapes, Liversage (2020) created experimental disturbances to initiate successional processes. They cleared 20 boulders mechanically by scraping off the biomass with a hammer; and 20 chemically, using hydrochloric acid. After two months they compared the species assemblage of the 40 disturbed boulders to 40 control ones through photographs of a 2 cm × 2 cm area of each boulder. This is similar to some of the disturbance experiments seen in previous chapters, for example the grazing/burning experiments at Konza (Raynor et al., 2015) in Chap. 6, or the herbicide treatments at Jena in Chap. 7 (Vogel et al., 2019). One manipulation of patch characteristics that appears to be more common in benthic seascapes than in terrestrial landscapes is the creation of experimental vegetation patches. The “mesocosm without walls” experiment by Chacin and Stallings (2016) described above used polypropylene ribbon tied to plastic mesh to simulate seagrass. In a similar experiment to test how the complexity of soft coral structures affected the ability of prey fish to be vigilant, Rilov et al. (2007) constructed devices made of PVC pipe frames to create a circular “curtain” of black nylon strips around focal fish nests. As a control, they used an identical device, but with transparent strips and another that only used the base frame of the device. They justified the use of strips to mimic the movement in the water of soft corals, because manipulation of live coral would be destructive and difficult to standardize (Rilov et  al., 2007). Others have used artificial seagrass as a way to provide a similar physical environment in terms of light levels and currents, without the benefit of a food source, to tease out how seagrass (Posidonia oceanica) canopy and patch-edge contrast affected sea urchin (Paracentrotus lividus) density (Pinna et al., 2013). Bell et al. (1988) placed artificial seagrass beds at different distances from the mouth of an estuary to disentangle the effects of location vs. seagrass bed attributes on larval settlement. In observational experiments, they noted differences in which species of larvae settled in different parts of the estuary, but because seagrass beds varied in their structure at different locations, they needed the manipulative experiment of artificial beds to standardize this effect. In a similar experiment, Nagelkerken and Faunce (2008) constructed artificial mangrove root structures with iron rods and black shading fabric, and placed these along a depth gradient to disentangle the effect of mangrove root structure and location (since mangroves are always in shallow water and sheltered locations) on fish species richness and abundance. They

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found that the attractiveness of the prop roots was a key driver – and not just the fact that they occurred in shallow, sheltered bays, which contrasts with the findings of Bell et al. (1988), who found that species responded more to location in the estuary than the physical attributes of the artificial seagrass beds. Researches have also used artificial seagrass patches to conduct experiments about patch size, shape and isolation in ways very similar to those we saw in Chaps. 6 and 7. For example, Jelbart et al. (2006) created three sizes (1 square and 2 rectangles) of artificial seagrass patches, of which two had the same area but different perimeter (the square and the large rectangle), and two had the same perimeter but different area (the square and the small rectangle). They placed these on a bare substrate in an estuary and sampled them for fish after 39 days to see how patch size and edge effects affected fish species richness. Eggleston et al. (1998) experimentally manipulated patch size (4 levels, the largest of which was bigger than most of the naturally occurring patches) and habitat type (artificial seagrass and trays filled with dead oyster shells) on recruitment of various species of grass shrimp as well as blue crab (Callinectes sapidus) larvae. Because they were looking at the effect of larvae in a dynamic system, they only required the artificial patches to be in situ for 14 days to see a response from their target organisms. They were also able to replicate each treatment three times along a transect (Eggleston et al., 1998). These systems can address questions that will be familiar to terrestrial conservation biologists. For example, McNeill and Fairweather (1993) used patches of artificial sea grass where the area of two small units equalled one large one to experimentally address the SLOSS (single large vs. several small) question for reserve design in a marine context. In their system (a shallow bay in New Zealand), they found very few significant differences in species recruitment between two small vs. one large artificial patch. However, they pointed out that their artificial patches were at the small end of the range of patch sizes typical for their study area, illustrating that scale considerations (Chap. 5) are important in all types of experiments. In North Carolina, USA, Micheli and Peterson (1999) assessed how corridors affected crab consumption of bivalves using enclosures placed over two oyster beds that were either connected by a strip of seagrass, or separated by un-vegetated substrate. They found that the vegetated strip of seagrass facilitated crab movement and predation. Strategic placement of exclosures, as done here to facilitate a corridor experiment, is a further way to manipulate patch quality for benthic organisms. Irlandi and Crawford (1997) manipulated patch quality by placing enclosures strategically so that they either had half intertidal saltmarsh substrate/half seagrass or half intertidal saltmarsh/half un-vegetated sediment and observing captive pinfish growth. Boström et al. (2011) provide a comprehensive review of patch-based studies in coastal environments, and emphasize the scaled, hierarchical nature of these environments in various environments, including salt marshes, coral reefs, mangroves, seagrass beds and oyster reefs. The majority of papers they reviewed are either field observations or models, and they documented field-based experiments most often in seagrass beds and oyster reefs, with a few occurring in salt marshes and coral reefs. A potential limitation is that most studies were short duration and

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had limited to no spatial or temporal replication (Boström et al., 2011). This may be due to the logistical challenges and dynamic nature of marine environments. While we can see that benthic environments, in particular shallow ones, are amenable to experiments, particularly those centred around questions about patch quality or context, the nature of the seascape environment poses logistical challenges that are absent in the terrestrial environment. To set up and monitor experiments often requires SCUBA diving, which is a specialized and expensive activity. As well, benthic environments, especially near shore ones, are subjected to a great deal of energy from waves and tides, which can easily destroy experimental set ups. It is no wonder then that many spatially explicit seascape research questions rely on observational studies, or make use of natural experiments, such as comparing samples taken in and outside of a marine protected area (Boström et  al., 2011; Rees et al., 2018; Marley et al., 2020). In the pelagic zone, the three-dimensional nature of the water column, coupled with rapid dynamics, makes it a different arena for experimentation than the benthic component of the seascape. However, tracer experiments in the pelagic zone are quite common, particularly on larger bodied organisms such as sea turtles (see review in Godley et  al., 2008) and marine mammals (e.g., Andersen et  al. 2013; Pérez-Jorge et  al., 2020). In early research, researchers tagged marine mammals with numeric or colour-coded identification markers, which only yielded the individual’s location information at mark and recapture/re-sight sites (Godley et  al., 2008). Early versions of satellite tags in the late 1980s gave the position of the animal each time it surfaced, which limited the analysis to their space use in two dimensions. Passive acoustic sampling is another technique that can be used to monitor fish movement in response to different habitat attributes (e.g., Hitt et al., 2011). Today, more sophisticated tags can record data on dive depth and duration, as well as heading, pitch and roll which allows for three- and four -dimensional modelling (Hazen et al., 2009; Andersen et al., 2014; Fortune et al., 2020). Andersen et al. (2014) used data on the ascent rate of hooded seals (Cystophora cristata) to identify “drift dives”—that describe when the animal is neutrally buoyant because it is resting or processing food. They also were able to integrate data on bathymetry, seasonality and first-passage time (the time it takes an individual to cross a circle of a given radius; determined by its average area-restricted search) to explain aspects of the three-dimensional space use (i.e., dive depth and duration) (Andersen, et al., 2013). Terrestrial landscape ecologists have similarly used first-passage time analysis with GPS collared ungulates to asses movement patterns in response to landscape pattern in a forest-agricultural matrix (Williams et al., 2012) or in response to spatial heterogeneity in foraging opportunities and predation risk (Frair et al., 2005). Tracer experiments with smaller organisms such as plankton and larval stages of various marine organisms require different tools, as these are too small to support telemetry devices. Instead, researchers have used genetic and chemical signatures (e.g., Leis et al., 2007; McMahon et al., 2012) and mark-re-sight techniques (e.g., Almany et  al., 2017) to detect dispersal of these smaller organisms, often across large spatial extents. As well, in silico models (e.g., Treml et al., 2012, 2015) coupled with observational tools such as spatial genetics (e.g., Liggins et al., 2016) are

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used to assess how seascape biophysical drivers affect dispersal of these types of organisms. Despite the fact that the marine environment is a challenging environment for experimental ecologists, landscape ecologists wishing to carry out experiments in seascapes should be able to extrapolate many of their conceptual frameworks and experimental techniques and work on marine spatial questions. Obviously, collaboration with physical and biological oceanographers and marine biologists is essential to understand the environment and organisms of interest, as well as to identify which aspects of the seascape (e.g., tides, currents) might pose a risk to certain types of experimental setups. Investment in different kinds of tools (SCUBA equipment, acoustic and laser seafloor surveys, ROVs) than we use in the terrestrial realm will often be necessary, but many of the tools used in ocean-based research in physiological, population and community ecology might be harnessed to address more spatially-­explicit questions. This is where collaboration of landscape ecologists with other ocean scientists may be of mutual benefit. In many (but not all) of the papers cited in this section, the authors did not specifically frame their work as “landscape ecology” or as having an explicit spatial focus. Indeed, many of them do not appear in the journals in which we expect to see landscape ecology work. However, a landscape ecologist reading these can see opportunities to link to concepts in our discipline, such as patch dynamics, connectivity, scale, hierarchy, dispersal, and pattern-process links. Seascape ecology that truly married landscape ecology research with marine-themed work could enhance marine research while at the same time providing novel environments for experiments to landscape ecologists. The dynamic nature of the marine environment, and the short experimental time of many of the experiments discussed here may have advantages for informing the design of terrestrial experiments.

11.3  Experiments in Riverscapes In another example of a movement from a “dry” landscape to a “wet” one, Wiens (2002) called for riverine systems (“riverscapes”) to be treated as entities in their own right for spatially-explicit research. While in some contexts it is appropriate to consider the interactions between terrestrial and aquatic environments, Wiens (2002) pointed out that river systems on their own have patch structure, just as terrestrial landscapes do. Riverscape patch structure is characterized by differences in water depth, channel width, and water velocity, as well as bottom substrate instead of landforms or land cover. Wiens (2002) proposed that several themes in terrestrial landscape ecology could be applied in riverscapes: an assessment of differences in patch quality; an investigation into how patch boundaries affect flows of energy material and organisms; and the influence of patch context, connectivity, diversity patterns, and scale. Wiens’ paper appears in a special issue in the journal Freshwater Biology (April 2002), devoted to the topic of riverine landscapes. The other papers in the issue describe geomorphic (Church, 2002; Richards et  al., 2002) or

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biodiversity (Adis & Junk, 2002; Buckton & Ormerod, 2002; Johnson, 2002; Malmquist, 2002; Robinson et  al., 2002) characteristics of riverine landscape. In addition there are articles on remote sensing methods for riverscapes (Mertes, 2002) and articles describing abiotic and biotic interactions within river systems and between the river and the surrounding landscapes (Dahm et al., 2002; Gurnell & Petts, 2002; Malard et al., 2002). Such descriptive work at the early stages of a new field of research is not surprising, and echoes some of the early types of articles in the field of landscape ecology (Wu, 2017). Despite nearly two decades since Wiens (2002) proposed that landscape ecologists take an explicitly “riverine” focus, there has been very little spatially explicit experimental work in river systems. Many of the studies that reference his work are observational experiments or modelling papers.1 This may be due in part to the challenge in manipulating river environments. In one ambitious manipulation to test whether sources of dissolved carbon in freshwater streams came from groundwater or via photosynthesis, Gray et al. (2011) covered a 36 m long reach of five separate streams with transparent polythene from the spring source (where water would carry dissolved carbon from the soil and/or bedrock) to downstream. The sheet prevented off-gassing, but allowed photosynthesis to continue. After sealing off the stream for an hour, they sampled water at four distances downstream of the spring for dissolved carbon content. They then removed the polythene sheet and manually removed all the photosynthetic organisms possible (all macrophytes, bryophytes and algae mats and any substrate with obvious diatoms) from the same 36 m stretch to assess how dissolved carbon changed. They then put the sheet back in place to see what occurred in the absence of both out-gassing and photosynthesis. Their statistical analysis accounted for the differences inherent in the five streams by first standardizing the post-treatment measures relative to the value at the source of each stream, and then treating the stream as a random effect in a linear mixed effects model (Gray et al., 2011). They found a decrease in dissolved carbon without both out-gassing and photosynthesis, but only outgassing has a statistically significant effect. Thus, they were able to illustrate that gradients of dissolved carbon in a steam system (gradients being a landscape ecology concept) are driven mainly by out-gassing (Gray et al., 2011). In another labour-intensive experiment that represents a fuzzy boundary between a mesocosm experiment (Chap. 8) and an in situ experiment, Olden et al. (2004) set out to test how current velocity interacted with landscape patch-pattern to facilitate movement of the grazing caddisfly (Agapetus boulderensis) larvae. The researchers

1  I searched all 586 papers that cited Wiens (2002) in Scopus that fell in the Subject Area of “Agricultural and Biological Science” (n = 368), for the term “experiment*” (n = 192) in either the title, abstract or keywords. Other than two papers calling for experiments to bolster a particular riverscape concept (Rolls et al., 2013; Hough et al., 2019), and two describing mesocosm experiments within riverscapes (Hoffman et al., 2006; Magierowski et al., 2015), I was able to find only 2 papers that described spatially-explicit experiments in riverscapes (Olden et  al., 2004; Gray et al., 2011). I discuss these above. In addition there was one paper describing a planting experiment in wetlands that included a treatment in riparian wetlands (Ström et al., 2014).

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created small arenas consisting of 14 rows and 14 columns of small, unglazed porcelain tiles (total arena size 185 cm × 60 cm) within an artificial stream channel. They cultured some tiles in situ in the stream to create uniform algal mats that presented “patches” for their study organism (caddisfly larvae) to both feed on and move through easily. They placed the other tiles in an experimental channel at a lower water velocity to which they added larvae of a Chironomid (Pagastia partica). The chironomids built silken “retreats” at high densities on the tiles – which represented “non habitat” to the caddisfly larvae and a barrier to their movement (Olden et al., 2004). The researchers then arranged these two tiles (“habitat” and “non habitat”) in a 2 x 2 factorial experiment that echoes some of the manipulations of habitat cover and fragmentation we saw at larger extents in the Bowling Green experiments (With & Pavuk, 2011) and in silico with the neutral landscape models (Gardner, 1999). Their factors were habitat amount (20, 40, 60, 80 and 100% of the arena covered in “habitat” tiles, with two random arrangements of the patches at each habitat level) and two levels of current velocity in the arena (facilitated through hoses running water from the natural streambed across the arena). Similar to With’s grasshopper experiments (With, 1994) that tracked movement with pins, observers watched an individual caddisfly larva in each arena for an hour and marked movement on a recording map that matched the pattern of the treatment (Olden et al., 2004). The unit of replication was the individual larva (10 individuals per treatment combination) and they did not treat these as random effects in the statistical analysis. Thus, inference is limited to the 200 individuals in the experimental arenas. Nonetheless, Olden et al. (2004) found a significant effect of habitat amount, current velocity, and the interaction between them. Because the replication is the individual larva and there was not replication of the different patch patterns, the study is unable to test how spatial configuration of the patches affected movement. Olden et al. (2004) included a spatially explicit analysis of movement pattern (i.e., proportion of movement steps in upstream vs. downstream directions) and their experimental set up could easily be modified to focus on the effect of variation in the landscape pattern and not simply the configuration. Their work—though somewhat dated and with some issues concerning replication and statistical analysis—has value in that it demonstrates a creative way to do manipulative experiments that have a “landscape ecology” question in river systems. Other river ecology research has recognized the importance of considering spatial context, without explicitly citing Wiens (2002). For example, McNeely and Power (2007) considered how landscape position in seven sites within a single drainage in northern California affected variation in the impact armored grazers (aquatic insects which have a stone case or shell) had on algae density. Their experiment consisted of paired exclosure/control tiles, coated with algal biofilms through natural exposure in each site. The stream sites varied in the physical dimensions (width, upstream drainage areas) and abiotic characteristics (canopy cover, water temperature) as well as which species was the dominant grazer. McNeely and Power (2007) treated site as a random effect, though interestingly (in reference to Chap. 4), they noted that their qualitative results were the same whether they treated sites as a fixed or a random effect. Their results showed site-level differences in primary

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productivity as well as in the impact of grazers, illustrating the importance of landscape context (McNeely & Power, 2007). Winemiller et  al. (2010) provide a thorough overview of the development of research in river systems that addresses patch dynamics. They argue that the concept of patch dynamics in river systems is supported by two (inter-related) concepts; a landscape perspective (Wiens, 2002) and a metacommunity perspective. Many of the experiments they cite that address questions around patch dynamics are observational, and they cite a need for improved quantitative methods as a key challenge for doing riverscape research (Winemiller et al., 2010). One quantitative landscape ecology tool that has translated well to riverscapes is that of connectivity. Anthropogenic barriers such as culverts and dams impede fish movement and thus have an impact on riverscape connectivity (Schick & Lindley, 2007). However, the dendritic topology of river systems means that connectivity metrics and tools that are used in the terrestrial environment that assume movement in all directions (e.g., lattice networks (Watts & Strogatz, 1998), neutral landscape models (Gardner et al., 1987), FRAGSTATS metrics (McGarigal & Marks, 1995)) do not work in riverscapes. Researchers have proposed a variety of indices to quantify riverscape connectivity; Jumani et al. (2020) review 29 metrics for river fragmentation. However, when considering the impacts of already-built infrastructure on riverscape connectivity, most studies are observational experiments that compare connectivity metrics in different watersheds to observed aquatic species richness and distribution. Within riverine systems, fish movement has been a dimension of connectivity more amenable to manipulative experiments, specifically, experiments to assess the effect of modifications to barriers on fish passage. For example, Naughton et  al. (2007) modified the construction of two weirs by adding panels that restricted flow and compared movement of tagged fish in the modified weir to a control condition that had the modified panels removed. Their analysis focused on whether the presence or absence of the additional panels affected the route the fish took through the transition pool, and the time it took them to pass. Their study focused on a control-­ treatment on the weirs themselves, and did not consider the full landscape context. In a full BACI (before-after-control-impact) experiment, Mahlum et al. (2018) pit-­ tagged fish in four watersheds in Newfoundland, Canada,  and set up detection arrays upstream and downstream of one culvert and one control area of each stream. They monitored fish movement across each detection array to assess how much of a barrier each culvert was, and under what kind of hydrological conditions. After culvert restoration, they compared three metrics (fish passage success, range of passable flows, and available passable flows) in the culverts. Their analysis showed that interpretation of success varied with the response used, and that interpretation gained from a full BACI was sometimes inconsistent with the interpretation that would have been made had they simply done a before-after (B-A) or a control-­ impact (C-I) study. This echoes the conclusions of an extensive review by Christie et al. (2020) who showed that BACI studies had less bias than B-A or C-I studies. Others have evaluated fish movement experimentally in flume tanks (e.g., Castro-­ Santos, 2005; Kemp et  al., 2011); these could be considered examples of a

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“microlandscape” experiment (which are discussed below) as well as a vector manipulation experiment (Type IV.14) as described by Jenerette and Shen (2012). It seems that the challenges to doing “landscape ecology” experiments (at least manipulative ones) in riverscapes are different from those in seascapes, despite the fact that both are inhospitable environments for lung-breathing scientists to work in. Rivers do not carry the same limitations of deep depth that the ocean does. At the same time, they do not have the same “expansiveness” that make the benthic landscape of the ocean somewhat familiar to us. Rather, their dendritic topology creates challenges for spatial orientation. Within a single river, sample sites quite close together but in different reaches can be much more different than sites a similar distance apart on the seabed. At the same time, it is more difficult to assert statistical independence confidently between sites, since downstream sites receive many inputs (nutrients, organisms, contaminants) from their upstream counterparts. Each watershed is also its own unique riverscape, so trying to standardize sampling by stream-order location across watersheds raises the challenge of replicate landscapes that I introduced in Chaps. 3 and 4. As we saw above, when considering measuring riverscape connectivity, the dendritic topology of rivers meant that researchers had to invent new metrics (e.g., Cote et  al., 2009), because terrestrial metrics would not work. Some readers of this text might be familiar with the river continuum concept (Vannote et al., 1980), which emphasizes the gradient of physical conditions and associated biological responses along the length of a river. Winemiller et al. (2010) suggest two alternative concepts that might aid more spatially explicit research. The first, the Process Domain Concept (Montgomery, 1999), focuses on the influence of geomorphic processes in forming patches within a watershed and driving the disturbance regimes. Terrestrial ecologists are familiar with how geomorphology and disturbance create patch pattern, so this concept should be easy to translate to a river system. The second, the Hierarchical Patch Dynamics Concept (Poole, 2002), will also be relatable to terrestrial landscape ecologists. It emphasizes the hierarchy of patches in a watershed, interacting with each other from headwaters to mouth, both within and across scales, and through links between process and function. Landscape ecologists seeking to branch out into experiments in riverscapes would be wise to familiarize themselves with these concepts.

11.4  Experiments in Soundscapes Soundscape ecology is an area of research that bridges several disciplines: acoustics, animal behaviour and landscape ecology (Pijanowski et  al., 2011; Farina, 2014). Soundscapes are characterized by three different sources of sound – biological ones such as bird song (biophony), abiotic ones such as wind or running water (geophony) and human ones such as traffic (anthrophony) (Fig. 11.2). In an introduction to a special issue of Landscape Ecology focused on soundscape ecology, Pijanowski et  al. (2011) outline how soundscape ecology has intellectual

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Fig. 11.2  A schematic of a soundscape, composed of biophony (green stars), geophony (blue stars) and anthrophony (brown stars). (Photo by Yolanda Wiersma)

foundations in spatial ecology, psychoacoustics, bioacoustics and acoustic ecology. They clarify that soundscapes reflect many ecological processes and are themselves patterns of sound. Soundscape ecology differs from the underlying and integrated fields of study in that it focuses on spatial and temporal variability in sound patterns, sound composition across scales, and the interactions between organisms and sound in space and between physical attributes of the landscape and sound proliferation (Pijanowski et  al., 2011). Nonetheless, many of the experimental approaches in soundscapes (including those described here) draw extensively on the antecedent disciplinary frameworks, and as we saw in the seascape section above, not all the papers described below necessarily identify as “-scape” research. However, I highlight papers where researchers have made use of space, either implicitly or explicitly, to illustrate the types of experiments possible in this novel landscape. It will also not be surprising that experiments in soundscape ecology involve the use of audio equipment. While behavioural ecologists have used audio recordings and playback experiments to develop an understanding of animal communication, soundscape ecologists explicitly address how space affects the use of sounds by animals, or how the landscape affects the transmission and perception of sounds. For example, Kight and Swaddle (2015) investigated how eastern bluebird (Sialia sialis) song changed in response to human disturbance. They used playback to stimulate songs in 60 different breeding territories and recorded ambient noise and habitat structure. They found that male bluebirds modified their song in response to anthropogenic changes in habitat structure (for example, amount of buildings, amount of impervious surface) as well as ambient noise in their territory (Kight & Swaddle, 2015). While theirs was a natural experiment, it illustrates one of the frequently confounding effects in studies that try to quantify the impact of anthrophony

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on organisms; frequently anthropogenic sounds coincide with anthropogenic changes to habitat. Deciding whether the observed response (be it changes in vocalization, fitness, occurrence, etc.) is due to the structural habitat changes, or the sounds, or an interaction between them can be tricky. Rosa et al. (2015) developed an innovative experimental approach to disentangle impacts of anthropogenic noise from physical anthropogenic impacts. They recorded sounds from oil well infrastructure in Alberta, Canada, and designed a solar-­powered playback system capable of continuous playback over the entire breeding season of grassland songbirds (3 months). They placed six of these (three each playing the sound of one of two types of equipment) in 64 ha mixed-grass prairie sites. By comparing recorded sounds from real equipment at intervals along a 100 m transect to recordings taken along a similar transect from the playback arrays, they were able to show that the characteristics of the sound from their experimental playback system was similar to sounds from real equipment. Thus Rosa et al. (2015) were able to create  an anthropogenic soundscape independently of physical anthropogenic impacts. Curry et al. (2018a) leveraged this experimental soundscape tool to asses how the well-drilling sounds affected songs of two grassland sparrow species. Because they could control the timing of the anthropogenic sounds, they were able to record bird song before, during and after the playback to determine whether and how the birds changed their song. They found that both species changed their song frequencies, but in different ways. The paper describing the experimental set-up by Rosa et al. (2015) also detailed a “control” system that included identical recording equipment, but which did not broadcast, as a way to assess species responses to the presence of the experimental infrastructure independent of the sound. Beyond physical infrastructure, another environmental feature where the organisms’ response can be confounded with sound is light, particularly around roads. To disentangle the impacts of sound vs. light on songbirds, Hennigar et al. (2019) conducted an experiment with three treatments (sound but no light, light but no sound, both sound and light) and a control (no sound, no light), each replicated between 17 and 39 times. The researchers implemented the sound treatment through an amplified speaker that broadcast a range of traffic sound, played for 15 hours continuously. They added light to the site with a battery-powered “Super Bright” LED suspended from a tree branch and programmed to turn on at dusk and off at sunrise. They found that response to light and/or sound was species-specific, with some attracted to either light or sound, and others avoiding it (Hennigar et al., 2019). Assessing how soundscape affects organisms could be considered an example of a manipulation of patch characteristics (Type III.7  in Jenerette & Shen, 2012). Researchers have carried out these experiments to assess the impact of soundscape manipulation on different types of organism responses, including changes to song type, as described above. Others have measured stress levels in birds (e.g., Curry, Des Brisay, et al., 2018b), bat feeding behaviour (e.g., Finch et al., 2020), zebrafish movement (e.g., Shafiei Sabet et  al., 2016), or mollusk larval recruitment (e.g., Lillis et al., 2015). Finch et al. (2020) carried out a BACI study of the effects of road sounds on horseshoe bats (Rhinolophus ferrumequinum) in England. They controlled for the confounding effects of road sounds vs. road infrastructure (pavement

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and lights) with playback experiments of road sounds along linear hedgerows and treelines. They monitored bat activity and bat calls for two nights with no sound playback (“before”) and for three treatment nights (“after”) where they played sounds for 3.5  h. To enable a full comparison, they compared the measurements from these sites (“impact”) to “control” hedgerows and treelines nearby (but far away enough to not be affected by the playback noise) (Finch et al., 2020). Much soundscape work has focused on terrestrial bioacoustics and behavioural ecology work on birds. A soundscape approach that integrates these fields with landscape ecology concepts will facilitate research on the spatial dimensions of sound. For example, considering how latitudinal, elevation, or edge-to-interior gradients affect the production and transmission of sound, as well as organisms’ response to sound requires tools in spatial analysis developed in landscape ecology (Pijanowski et al., 2011). Sound is an important component of seascapes and coastlines as well. Lillis et al. (2015) deployed underwater speakers with and without sound to assess how reef sounds (recorded on a natural reef in Pamlico Sound, USA) affected larval settlement of oysters at two experimental sites on a mud flat. In a similar experiment on the Great Barrier Reef, Simpson et al. (2008) played reef sounds above artificial reef patches, with a parallel “dummy” set up to test if fish used reef sounds to navigate onto reefs after nocturnal movement. While some of these experiments are more behavioural, they do manipulate sound over space, and one could combine such experiments with manipulation and/or data collection of other spatial variables to conduct more spatially explicit “soundscape” experiments. Soundscape ecology also has potential to harness spatial tools such as GIS to map sound or create soundscape information systems (see “Resources” section for details), which in turn can contribute to management and conservation initiatives where human activities and noise are adversely affecting organisms (Pijanowski et al., 2011). Although human aural perception is different from other organisms, sound plays an important role in our enjoyment of an area. In a perception experiment (Type I.1 in Jenerette & Shen, 2012) aimed at assessing how people perceived “wildness” in the United Kingdom, Pheasant and Watts (2015) showed volunteers short video clips of sixteen different areas, including open vistas in the Scottish Highlands, wild rivers, along roads and railways, and in the centre of a busy village. The views of these were edited to contain either enhanced natural sounds (either biophony such as bird song or an elk call, or geophony such as wind or moving water), or enhanced anthrophony (traffic, overhead aircraft, farm tools). Twenty-one volunteers watched these video clips (in a randomized order among volunteers), and rated their perception of each scene in terms of the wildness, tranquility, naturalness and “felt remoteness”. Pheasant and Watts (2015) found that the additional sounds (whether anthropogenic or natural) resulted in significant differences in viewers’ ratings over the controls, which were the videos with the sound “as recorded” in situ. Their findings suggested that anthropogenic sound affected people’s perceptions of tranquility and wildness, although with a fair degree of inter-observer variation (Pheasant & Watts, 2015).

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Others have used soundscapes in perception experiments using virtual reality (VR) to assess perceptions of different potential designs of a footbridge over a highway (Echevarria Sanchez et al., 2017) or the impact of a proposed highway (Ruotolo et al., 2013). In the former example, Echevarria Sanchez et al. (2017) created virtual realities of different kinds of noise barriers along the bridge, that differed in their aesthetics and their ability to buffer the traffic sound underneath. The immersive nature of the VR-experience allowed the researchers to match the sounds participants experienced with the different sound barriers they “walked” through, thus making their rankings of preference for the different bridge designs more realistic. In a Virtual Reality B-A (before-after) design, Ruotolo et al. (2013) created pre- and post-highway construction landscapes in an otherwise rural landscape, and recorded ambient sounds to match three different distances and directions from the highway. They then added a highway to their virtual world coupled with real highway sounds, as the viewer would perceive them from the three locations. Participants “visited” each of the three sites in the VR landscape in simulations that represent both “before” and “after” construction of the highways. After each visit, the participants were asked to perform a variety of cognitive tasks, and the researchers assessed how sound and visual stimulation of the highway affected cognitive performance (Ruotolo et al., 2013). They showed that sound could have a detrimental effect on cognitive abilities but that this was dependent on how close the participant was to the sound source. In an innovative approach to a perception experiment, Borker et al. (2020) used soundscapes as an adaptive management tool to assess restoration success. Following removal of invasive rat and fox predators on the Aleutian Islands, researchers wished to quantify the impact of the restoration activity on seabird colonies. The remote and rugged nature of the islands made in-person monitoring difficult, and so they deployed acoustic recorders across 13 sites on four islands that had had successful predator eradication. They developed indices of acoustic diversity and compared these to a control island that had never had predators, and one where rats were still present. Borker et  al. (2020) were able to characterize the soundscapes of each site using a suite of indices and found that the soundscapes on the restored islands more closely resembled the reference island, and that time since restoration explained nearly 30% of the variation in the differences between islands. Thus, without directly counting or monitoring seabird colonies, they could used soundscape indices to assess the state of the islands, and over a longer period of time and a wider extent than a team of human researchers would have been able to monitor. Soundscape experiments are technologically intensive. Fortunately, for anyone embarking on this as a new research area, there are many useful methods papers available (see Resources section). Because researchers have been recording animal sounds to understand communication and behaviour for decades, there are well-­ established tools and protocols for conducting playback experiments, carrying out effective recording in the field, and analysing spectrogram data. Many of these will be specific to the organisms of interest, as the vocalization of birds, anurans, primates and marine mammals are very different from each other. In terms of spatial

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approaches, recent technology allows very high precision triangulation of a bird’s position in three dimensions using wireless microphone arrays (Mennill et  al., 2012). Indices to quantify soundscape pattern, such as those used by Borker et al. (2020) in the Aleutian case study above (and see also indices described in Gómez et al., 2018) can be useful ways to quantify soundscape variation in space and time, although one should be mindful of the limitations of indices. For example, Sandoval et al. (2019) suggest that the Shannon-Weiner Entropy Index does not adequately quantify acoustic diversity and that other metrics are more appropriate.

11.5  Experiments in Micro-landscapes Micro-landscapes are artificially constructed landscapes that act as experimental arenas. Larsen and Hargreaves (2020) developed this definition in an in-depth review of how micro-landscapes are a useful tool to understand species distributions. Their argument for using micro-landscapes in biogeography echoes many of the points in Chap. 3 of this book; namely, that real-world landscapes are difficult to replicate, and many processes at “typical” landscape scales play out over longer periods than is feasible for experimentation. They argue that scaled-down experiments allow for controlled manipulation and can take advantage of working with organisms with fast generation times so that researchers can obtain responses to the manipulations quickly. Micro-landscapes share many similarities with mesocosms (Chap. 8) and microcosms (Chap. 9), but differ in that they generally are used in a lab setting, and are for the most part artificial. Many of them use microorganisms such as bacteria, protists, or smaller organisms such as arthropods and nematodes (Larsen & Hargreaves, 2020); organisms not often studied in landscape experiments in the real world. As we saw in Chaps. 8 and 9, these definitions to discriminate between microcosms, mesocosms and micro-landscapes are fuzzy; for example, Larsen and Hargreaves (2020) include the moss patch experiments (Gilbert et al., 1998; Gonzalez et al., 1998) which I classified as microcosms as examples of micro-­ landscapes in their review. The key point is that micro-landscapes are a type of model landscape, and can be considered a model system (Larsen & Hargreaves, 2020), much as Srivastava et al. (2004) proposed for microcosms. Zuk and Travisano (2018) discuss different types of models in scientific research; this can include scaled-down replicates, theoretical abstractions (an example in landscape ecology would be the patch-mosaic model), mathematical constructs (neutral landscape models in our field), or model organisms (e.g., Drosophila in genetics). While in some cases, the intent of using models is to eventually extrapolate to the real world, Zuk and Travisano (2018) point out that models are not always intended to represent the real world and that over-generalizing from a model can be dangerous. Echoing John Wiens’ influential scaling paper (Wiens & Milne, 1989), Zuk and Travisano (2018) point out that, in some cases, scaled-down systems, such as flour beetles in a storage container, represent the “real world” from the perspective of that organism. This is why, in Chap. 8, I treated the experiments with grain

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borers between plates of glass as mesocosms, since they represented containerized delineations of the grain borers’ natural environment. Nonetheless, model systems can be useful, as they may be simplified representations of more complex systems (Vitousek, 2002; Srivastava et al., 2004; Ankeny & Leonelli, 2011; Zuk & Travisano, 2018) that may have faster processes, be smaller and easier to manipulate experimentally, and yet share ecological and evolutionary qualities with larger systems. Micro-landscapes represent “constructed landscapes” (Type III.12 in Jenerette & Shen, 2012), and can be manipulated to test different kinds of spatial questions. The review by Larsen and Hargreaves (2020) focused on micro-landscapes that touched on issues of species distribution, and highlighted several experiments that deal with biogeography (and landscape ecology) concepts such as dispersal, gradients, and patch structure. Many micro-landscape constructions can manipulate connectivity (Experiment Type III.9 in Jenerette & Shen, 2012) quite easily, either by facilitating movement of organisms between “patches” (e.g., Carrara et al., 2012) or by adding physical connections, such as tubing or piping to connect containers for protozoa (e.g., Donahue et al., 2003; Altermatt et al., 2011). Others have examined functional connectivity (as opposed to structural connectivity). For example Stevens et  al. (2006) constructed experimental Y-shaped arenas (approximately 50 cm long) for natterjack toadlets (Bufo calamita). They released toadlets at the base of the “Y”; at the fork, the toadlet had to choose between continuing on a narrower branch, but that had a surface contiguous with that surface at the release point, and a wider branch that had a contrasting surface. The researchers combined different permutations of surfaces that mimicked what the toadlets might encounter in the real world, including natural environments, agricultural environments, roads, and sandy soil. By documenting toadlet movement and assessing under which conditions they exhibited boundary crossing from one substrate to another, the researchers could assess how permeable different environments were in the real world, to better assess functional connectivity. In addition to assessing connectivity, researchers can easily manipulate topology by rearranging the pattern of connections. For example, Altermatt and Fronhofer (2018) compared dispersal of ciliates (Tetrahymena pyriformis) in linear vs. dendritic networks by manipulating the spatial arrangement of their vial and tube set up, and Carrara et al. (2012) created dendritic and lattice networks using well-plates and systematically transferred the contents of each well to a neighbour in a prescribed pattern that mimicked different topologies. Fragmentation experiments (Type III.10 in Jenerette & Shen, 2012) have been carried out in micro-landscapes in a way that echoes some of the experimental model landscapes we saw in Chap. 7. Romero et al. (2009) created 50 cm × 50 cm arenas made of binary habitat (cells of flour patches) and non-habitat. They generated random landscape models using the same RULE software (Gardner, 1999) that researchers used in the Bowling Green experiments that I discussed in Chap. 7 (With, 1997, 2016; With & Pavuk, 2011, 2019). As in the Bowling Green experiments, Romero et  al. (2009) manipulated habitat amount and aggregation, and added a manipulation of grain size. These fragmentation studies represent how different experimental approaches  – in this case in silico experiments, large-scale

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experimental model landscapes and micro-landscapes, can complement each other and facilitate broader generalizations. The above example also illustrates how micro-landscapes can facilitate cross-­ scale experiments (Type III.11 in Jenerette & Shen, 2012). Results from Romero et al.’s (2009) replicated 50 cm × 50 cm landscapes can be contrasted with the replicated 16  m × 16  m landscapes at Bowling Green. For example, it is easier to manipulate patches in the micro-landscape and in the in silico environment (Gardner, 1999) than in other experimental venues. Others have scaled down both patterns and processes in micro-landscapes. For example, wildlife observations show that herbivores track phenological change in plants in space and time. However, experimentally manipulating variation in spatial and temporal patterns of food availability to elucidate mechanisms is difficult with wide-ranging ungulates. Searle et al. (2010) created six 30 m × 1.5 m micro-landscapes in which they manipulated the timing and spatial pattern (but not the amount) of food patches (pots of young wheat shoots) for their herbivore (a grasshopper) to test competing hypotheses for how resource availability in space and time affected herbivore growth and nutritional status. This allows for comparisons of results from these small-scale experiments to large-extent observations of movement of herbivores, such as red deer (Pettorelli et al., 2005) or wildebeest (Wilmshurst et al., 1999). Other highly feasible micro-landscape experiments include manipulation of patch quality (experiment Type III.7 in Jenerette & Shen, 2012) by changing the type or the amount of food resources in different patches (e.g., Donahue et al., 2003; Davies et al., 2009). It is also much more tractable to carry out a fully replicated multi-factorial experiment to test multiple drivers with micro-landscapes, since they are small, and can often be relatively inexpensive to construct and maintain. For example, Govindan and Swihart (2012) experimentally manipulated resource levels (constant vs. diminishing), patch configuration, and connectivity in a micro-­ landscape for flour beetles (Tribolium castaneum) constructed from 17 cm × 12 cm plastic boxes, with a flour-yeast mixture representing high quality patches, and powdered sugar representing low quality patches. While the materials used to construct micro-landscapes are quite low-tech, and often readily available, the challenge with micro-landscape research is ensuring the organisms stay alive for the duration of the experiment. Thus, researchers wishing to embark on micro-landscape studies will have to become familiar with methods to rear and maintain microorganisms in lab conditions. Kurkjian (2019) provides a detailed and highly useful methods paper for harnessing the 96-well plate for metapopulation experiments. Although many of the examples are more biogeographical than landscape ecological, the review by Larsen and Hargreaves (2020) is an excellent starting point to appreciate the breadth of approaches researchers have used to construct micro-landscapes.

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11.6  Atypical Landscapes Finally, if landscape ecologists really want to “think outside the box”, they can consider the landscapes they are carrying around within their own bodies! This may sound strange, but biomedical researchers have proposed that we consider parts of the human body as landscapes. Proctor and Relman (2018) point out that the human ear, nose and throat contain microbial ecosystems that have spatial heterogeneity and respond to gradients in the body’s microenvironment. In an article aimed at their peers, in the journal Cell Host & Microbe, they offer a primer on landscape ecology, and suggest that a landscape ecology “lens” could be beneficial to understanding the structure and function of microbial communities in the human body. They propose that actions like tooth brushing are a disturbance for the biofilms living on our teeth, but that there is variation in the impact based on the differences in the topographic heterogeneity of the surface of the sides vs. the tops of teeth. They document known variation in spatial pattern of bacteria in the mouth, and conclude that taking a landscape ecology view of the human body can help with “setting the stage for more mechanistically informed and predictive interventions in disease” (Proctor & Relman, 2018, p. 15). In a similar example, but one directly aimed at the disease of cancer, Lloyd et al. (2015) propose to colleagues reading Advances in Anatomic Pathology that a landscape approach can enhance precision treatment in oncology. They point out that cancer tumours display genetic heterogeneity within and between tumours, and that this genetic diversity reflects morphologically in the histology of the cells. They propose a new discipline of landscape pathology, which they define as one that applies “quantitative, spatially explicit methods from landscape ecology to define the heterogeneous biological processes of cancer cells (the ‘organism’) in histological samples (the ‘habitat’)” (Lloyd et  al., 2015, p.  267). This view builds on an ecological and evolutionary view of cancer, and seeks to consider cancer cells as organisms trying to persist and disperse in the landscape of the human body. For example, by thinking about cancer in an ecological niche modelling context (a concept familiar to landscape ecologists), Lloyd et al. (2015) suggest that it might be possible to understand and possibly mitigate the spread of cancer within the body. Similarly, Amend et al. (2018) consider cancer through the lens of foraging ecology. Spatial concepts of patch use and habitat selection are familiar to landscape ecologists thinking about how large-bodied mammals move across a kilometres-extent landscape, but Amend et al. (2018) point out that nutrients to support the growth of cancer tumours is heterogeneous in space, for example, due to proximity to blood vessels. Cunningham et al. (2021) defines cancer cells fitness is as a function of how their phenotype interacts with their local environment, which varies in space and time. This results in source-sink habitats for cancer cells, which in turn influences tumor evolution (Cunningham et  al., 2021). While cancer cells do not have the senses an organism has to perceive their habitat, an understanding of how resources to support (or inhibit) cancer spread, drawing on landscape ecology principles, can help manage this disease.

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Drawing parallels from cancer research back out to landscape ecology, Lloyd et al. (2015) suggest that histology slides or MRI images are analogous to the maps that landscape ecologists might use, and they encourage their colleagues to make use of many of the metrics and tools used by landscape ecologists to characterize and analyze patterns in oncology. While it is interesting and exciting to see medical researchers adopt a landscape ecology lens to improve human health, perhaps collaborations between researchers in medicine and ecology can benefit the landscape ecologists as well. Cell cultures and histological slides might represent a new kind of “micro-landscape” for us, one where there is a high amount of replication. Some of the spatial concepts applied to cancer research (e.g., source-sink dynamics; Cunningham et al., 2021) have only be modelled mathematically, and experiments could help advance knowledge in both the medical and landscape ecology disciplines. Ironically, considering “bodies as landscapes” may introduce a similar problem with replication we have with real-world landscapes, since, just as with landscapes, no two humans are identical. However, medical researchers are familiar with this inter-subject variation and incorporate this challenge into the design and statistical analysis of every clinical trial.

11.7  What Can We Learn from Novel Landscapes? This chapter has outlined some areas for research that may not be front-and-centre in the mind of many (but certainly not all) landscape ecologists: seascapes, riverscapes, soundscapes, micro-landscapes, corporeal and histological landscapes. Experiments in these very different environments offer opportunities to ask different kinds of questions and adopt different experimental techniques. I hope that by reading this, you realize that when it comes to how and where to do landscape ecology experiments, you are only limited by your creativity (and obviously, your research budget). On the budget front, some of the systems I have discussed in this chapter can be relatively inexpensive to work in, and perhaps some of them are right at your back doorstep. If you live along a coast or river, but have been travelling half-way across the continent to do field work on grassland ungulates, perhaps this chapter will inspire you to think about how you can experimentally address your burning research questions in environments closer to home. Even in the “typical” terrestrial landscapes in which many of us have been working, there is room to think a little bit outside the box. Landscape ecologists have characterized seascapes and riverscapes as “fast-moving landscapes”. However, if we think of how atmospheric processes move particulate matter and pollen around, the air masses above our terrestrial landscapes are also fast moving, and are not that different to the water masses that characterize and influence seascapes. Perhaps collaboration with atmospheric scientists will open up new areas for terrestrial landscape ecology research. Obviously, not every type of experiment can work in every environment. Studying physical landscape connectivity in a soundscape does not make much sense. Patch-­ level experiments in the pelagic part of the seascape may be less practical than in the

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benthos, and manipulating disturbance in a highly dynamic system like a riverscape may not yield satisfying results. However, by matching (or adapting) the research hypothesis to the environment, new arenas for rigorous experimentation may open up for you. As stated above, working in some of these novel environments will often require some interdisciplinary collaborations – with marine biologists, limnologists, acoustic specialists or medical experts. Landscape ecology takes pride in labelling itself as an “interdisciplinary discipline” so reaching out across these boundaries to embrace experiments in these novel landscapes should not be too big a stretch for any of us. Make friends and collaborators out of researchers in diverse fields, who share an interest in figuring out how and why “space matters”, and I predict exciting things will follow.

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Pérez-Jorge, S., Tobeña, M., Prieto, R., et al. (2020). Environmental drivers of large-scale movements of baleen whales in the mid-North Atlantic Ocean. Diversity and Distributions, 26, 683–698. https://doi.org/10.1111/ddi.13038 Pettorelli, N., Mysterud, A., Yoccoz, N. G., et al. (2005). Importance of climatolgoical downscaling and plant phenology for red deer in heterogenous landscapes. Proceedings of the Royal Society B: Biological Sciences, 272, 2357–2364. Pheasant, R.  J., & Watts, G.  R. (2015). Towards predicting wildness in the United Kingdom. Landscape and Urban Planning, 133, 87–97. https://doi.org/10.1016/j.landurbplan.2014.09.009 Pijanowski, B. C., Farina, A., Gage, S. H., et al. (2011). What is soundscape ecology? An introduction and overview of an emerging new science. Landscape Ecology, 26, 1213–1232. https://doi. org/10.1007/s10980-­011-­9600-­8 Pinna, S., Sechi, N., & Ceccherelli, G. (2013). Canopy structure at the edge of seagrass affects sea urchin distribution. Marine Ecology Progress Series, 485, 47–55. https://doi.org/10.3354/ meps10326 Pittman, S. J. (Ed.). (2018). Seascape ecology. Wiley Blackwell. Pittman, S. J., Wiens, J. A., Wu, J., & Urban, D. L. (2018). Landscape ecologists’ perspectives on seascape ecology. In S. J. Pittman (Ed.), Seascape ecology (pp. 485–492). Wiley Blackwell. Poole, G. C. (2002). Fluvial landscape ecology: Addressing uniqueness within the river discontinuum. Freshwater Biology, 47, 641–660. https://doi.org/10.1046/j.1365-­2427.2002.00922.x Proctor, D.  M., & Relman, D.  A. (2018). The landscape ecology and microbiota of the human nose, mouth and throat. Cell Host & Microbe, 21, 421–432. https://doi.org/10.1016/j. chom.2017.03.011.The Raynor, E. J., Joern, A., & Briggs, J. M. (2015). Bison foraging responds to fire frequency in nutritionally heterogeneous grassland. Ecology, 96, 1586–1597. https://doi.org/10.1890/14-­2027.1 Rees, M. J., Knott, N. A., Neilson, J., et al. (2018). Accounting for habitat structural complexity improves the assessment of performance in no-take marine reserves. Biological Conservation, 224, 100–110. https://doi.org/10.1016/j.biocon.2018.04.040 Richards, K., Brasington, J., & Huges, F. (2002). Geomorphic dynamics of floodplains: Ecological implications and a potential modelling strategy. Freshwater Biology, 47, 559–579. https://doi. org/10.1046/j.1365-­2427.2002.00920.x Rilov, G., & Schiel, D.  R. (2006). Seascape-dependent subtidal  – Intertidal trophic linkages. Ecology, 87, 731–744. Rilov, G., Figueira, W.  F., Lyman, S.  J., & Crowder, L.  B. (2007). Complex habitats may not always benefit prey: Linking visual field with reef fish behavior and distribution. Marine Ecology Progress Series, 329, 225–238. https://doi.org/10.3354/meps329225 Robinson, C. T., Tockner, K., & Ward, J. V. (2002). The fauna of dynamic riverine landscapes. Freshwater Biology, 47, 661–677. https://doi.org/10.1046/j.1365-­2427.2002.00921.x Rolls, R. J., Ellison, T., Faggotter, S., & Roberts, D. T. (2013). Consequences of connectivity alteration on riverine fish assemblages: Potential opportunities to overcome constraints in applying conventional monitoring designs. Aquatic Conservation: Marine and Freshwater Ecosystems, 23, 624–640. https://doi.org/10.1002/aqc.2330 Romero, S., Campbell, J. F., Nechols, J. R., & With, K. A. (2009). Movement behavior in response to landscape structure: The role of functional grain. Landscape Ecology, 24, 39–51. https://doi. org/10.1007/s10980-­008-­9278-­8 Rosa, P., Swider, C. R., Leston, L., & Koper, N. (2015). Disentangling effects of noise from presence of anthropogenic infrastructure: Design and testing of system for large-scale playback experiments. Wildlife Society Bulletin, 39, 364–372. https://doi.org/10.1002/wsb.546 Ruotolo, F., Maffei, L., Di Gabriele, M., et al. (2013). Immersive virtual reality and environmental noise assessment: An innovative audio-visual approach. Environmental Impact Assessment Review, 41, 10–20. https://doi.org/10.1016/j.eiar.2013.01.007 Sandoval, L., Barrantes, G., & Wilson, D. R. (2019). Conceptual and statistical problems with the use of the Shannon-Weiner entropy index in bioacoustic analyses. Bioacoustics, 28, 297–311. https://doi.org/10.1080/09524622.2018.1443286

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Schick, R.  S., & Lindley, S.  T. (2007). Directed connectivity among fish populations in a riverine network. Journal of Applied Ecology, 44, 1116–1126. https://doi. org/10.1111/j.1365-­2664.2007.01383.x Searle, K. R., Hobbs, N. T., & Jaronski, S. R. (2010). Asynchrony, fragmentation, and scale determine benefits of landscape heterogeneity to mobile herbivores. Oecologia, 163, 815–824. https://doi.org/10.1007/s00442-­010-­1610-­8 Shafiei Sabet, S., Van Dooren, D., & Slabbekoorn, H. (2016). Son et lumière: Sound and light effects on spatial distribution and swimming behavior in captive zebrafish. Environmental Pollution, 212, 480–488. https://doi.org/10.1016/j.envpol.2016.02.046 Simpson, S. D., Jeffs, A., Montgomery, J. C., et al. (2008). Nocturnal relocation of adult and juvenile coral reef fishes in response to reef noise. Coral Reefs, 27, 97–104. https://doi.org/10.1007/ s00338-­007-­0294-­y Srivastava, D. S., Kolasa, J., Bengtsson, J., et al. (2004). Are natural microcosms useful model systems for ecology? Trends in Ecology & Evolution, 19, 379–384. https://doi.org/10.1016/j. tree.2004.04.010 Steele JH (1989) The ocean “landscape.” Landscape Ecology 3:185–192. https://doi.org/10.1007/ BF00131537. Stevens, V. M., Leboulengé, É., Wesselingh, R. A., & Baguette, M. (2006). Quantifying functional connectivity: Experimental assessment of boundary permeability for the natterjack toad (Bufo calamita). Oecologia, 150, 161–171. https://doi.org/10.1007/s00442-­006-­0500-­6 Ström, L., Jansson, R., & Nilsson, C. (2014). Invasibility of boreal wetland plant communities. Journal of Vegetation Science, 25, 1078–1089. https://doi.org/10.1111/jvs.12157 Suski, J. G., Swan, C. M., Salice, C. J., & Wahl, C. F. (2018). Effects of pond management on biodiversity patterns and community structure of zooplankton in urban environments. Science of the Total Environment, 619–620, 1441–1450. https://doi.org/10.1016/j.scitotenv.2017.11.153 Treml, E. A., Roberts, J. J., Chao, Y., et al. (2012). Reproductive output and duration of the pelagic larval stage determine seascape-wide connectivity of marine populations. Integrative and Comparative Biology, 52, 525–537. https://doi.org/10.1093/icb/ics101 Treml, E. A., Ford, J. R., Black, K. P., & Swearer, S. E. (2015). Identifying the key biophysical drivers, connectivity outcomes, and metapopulation consequences of larval dispersal in the sea. Movement Ecology, 3, 17. https://doi.org/10.1186/s40462-­015-­0045-­6 Turner, M. G. (1989). Landscape ecology: The effect of pattern on process. Annual Review of Ecology and Systematics, 20(20), 171–197. https://doi.org/10.1146/annurev.es.20.110189.001131 Vannote, R. L., Minshall, G. W., Cummins, K. W., et al. (1980). The river continuum concept. CanadianJournal of Fisheries and Aquatic Sciences, 37, 130–137. Vitousek, P.  M. (2002). Oceanic islands as model systems for ecological studies. Journal of Biogeography, 29, 573–582. https://doi.org/10.1046/j.1365-­2699.2002.00707.x Vogel, A., Manning, P., Cadotte, M. W., et al. (2019). Lost in trait space: Species-poor communities are inflexible in properties that drive ecosystem functioning. Advances in Ecological Research, 61, 91–131. https://doi.org/10.1016/bs.aecr.2019.06.002 Watts, D. J., & Strogatz, S. H. (1998). Collective dynamics of “small-world” networks. Nature, 393, 440–442. Werner, E.  E., & Gilliam, J.  F. (1984). The ontogenetic niche and species interactions in size-­ structured populations. Annual Review of Ecology and Systematics, 15, 393–423. Wiens, J.  A. (1992). Ecological flows across landscape boundaries: A conceptual overview. In A. J. Hansen & F. Di Castri (Eds.), Landscape boundaries: Consequences for biotic diversity and ecological flows (pp. 217–235). Springer. Wiens, J. A. (2002). Riverine landscapes: Taking landscape ecology into the water. Freshwater Biology, 47, 501–515. https://doi.org/10.1046/j.1365-­2427.2002.00887.x Wiens, J. A., & Milne, B. T. (1989). Scaling of “landscapes” in landscape ecology, or, landscape ecology from a beetle’s perspective. Landscape Ecology, 3, 87–96. https://doi.org/10.1007/ BF00131172

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Chapter 12

Where to Go from Here?

Any time we do a series of experiments, there are going to be three or four new questions that come up when you think you’ve answered one. Carol W. Greider (American molecular biologist and Nobel laureate)

12.1  Doing Experiments Experiments are at the heart of what it means to “do science”. However, ecologists, with their strong roots in natural history, have sometimes struggled with how to reconcile their work with experimental approaches used by bench scientists who can rigorously control all aspects of their investigation (Kohler, 2002). This tension is evident in a 1957 Presidential Address to the British Ecological Society (BES), where G.C. Varley chastised his colleagues for “seeking remote places where they can study ‘natural habitats’” (Varley, 1957, p. 252), presumably motivated by natural history’s attitudes to discovery (and perhaps lingering colonialist attitudes). In his speech, Varley points out that visits to exotic locales are “too few and too short for the work to develop beyond a superficial and descriptive stage”. He goes on to stress that ecologists “must learn to use and understand experimental methods which provide the most powerful tools in scientific analysis, and use them to investigate the basic principles of ecology, which operate on animals and plants everywhere” (Varley, 1957, p. 252). Although more than a half-century has elapsed since Varley made this direct call for more experimentation to the BES, some of the issues presented to early ecologists (see summary in Underwood, 2009) are still faced in the newer sub-discipline of landscape ecology. Experiments, as a key part of the scientific method, are a way of knowing about the natural world. Yet, science is not the only form of knowledge, and I do not think we need to disown ourselves completely from our natural history roots. In her book Braiding Sweetgrass, Robin Wall Kimmerer, a Potawatomi woman trained in both © Springer Nature Switzerland AG 2022 Y. F. Wiersma, Experimental Landscape Ecology, Landscape Series 29, https://doi.org/10.1007/978-3-030-95189-4_12

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Indigenous and western scientific traditions, describes how Indigenous ways of knowing and connecting to the natural world interact with her scientific training. Her descriptions of various research projects that she has been involved in all emphasize the need to combine respect, reciprocity and humility with the rigor of doing science. Those of us who do not have (or may have lost) links to traditional ways of knowing might still have an innate affinity or a sense of wonder for our system or study species. Indeed, as Kimmerer (2013) states, she has “never met an ecologist who came to the field for the love of data or the wonder of a p-value”. Thus, while much of the development of experimental methods in the history of ecology as a science has emphasized moving away from natural history appreciation, we should not bury these affinities for the natural world completely. Most of us became ecologists because we like being outdoors, or have a passion for a particular group of organisms, whether these are fish, birds, insects, plants or lichens. In our quest for rigorous experiments, we should not forget what it is about particular landscapes or organisms that inspire and motivate us. In addition to not letting go completely of a sense of wonder for the natural world, a little bit of naïveté does not hurt. We do not want to tie ourselves so strongly to a particular hypothesis or experimental approach that we become blind to other insights. Nor do we want to be afraid of trying something new and different, as long as we have some reasons for thinking it might be a good idea. For example, Darwin talked about his love for “fools’ experiments”, such as when he placed an unfertilized female flower and pollen from a male flower in a bell jar to see if they would interact or when he fed bits of his own hair and toenails to a carnivorous plant. Though these seem like cavalier experiments, the depth of Darwin’s genius meant that he could knit these various insights (most of which he made close to his home at Down House) with observations made in the exotic locales visited by the HMS Beagle into support for his groundbreaking theory. A seemingly foolish experiment with careful thought behind it will yield more valuable insights than a careful experiment with no thought behind it. Thus, we should not be afraid to think outside the box when developing experiments. You also need to be ready to admit you are wrong when your experiment does not work out as planned. As the character Wonko the Sane, in Douglas Adams’ Hitchhiker’s Guide to the Galaxy puts it, “(y)ou can’t possibly be a scientist if you mind people thinking that you’re a fool”. At the same time, you want to do your experiments well; which has been the focus of this book.

12.2  Experiments in Landscapes In the opening chapter to this book, I suggested that it has been difficult to do experiments in landscape ecology, owing to the spatial complexity of landscapes and the large extent at which most landscapes are studied. The size of most landscapes can make it difficult, if not impossible to do manipulative experiments, and their complexity means it is challenging to design sampling in the same way as one would when working within a homogenous plot (Jenerette & Shen, 2012). Each

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landscape is unique, making it difficult to have replicate treatments between landscapes, or to extrapolate findings from one landscape to a broader context. The challenges of reconciling the complexity of natural systems with the rigour of experimental design mirrors the tensions between field and lab work in the early development of the science of ecology (Guidetti et al., 2014; Kohler, 2002), that are described in Chap. 2. Here, I emphasized that observational (also labelled “natural”) experiments are as equally valid as lab-based manipulative experiments (Diamond, 1983, 2001), which is critical, since many experiments in landscape ecology are, by necessity, observational. Nonetheless, all experiments should enable rigourous falsification. A strong grounding in the history and philosophy of science, as summarized in Chap. 2, is a necessary first step to doing good experiments (Betts et al., 2021). After this, one can determine how best to meet the criteria for good experimentation, which are control, randomization and replication (these have also been well-outlined by others, e.g., Hairston Sr., 1989; Underwood, 2009). In Chap. 3, I examined how these criteria could be challenging to achieve in landscapes owing to their size, complexity and the spatially explicit nature of many of the concepts and questions addressed by landscape ecologists. I discussed two aspects of experimentation that are particularly germane to landscape studies, pseudoreplication and scale, in Chaps. 4 and 5 respectively. As outlined in the opening section of the book, publications from the early years of the discipline of landscape ecology have emphasized pattern description and methodological developments, with few explicitly experimental studies making it to the list of highly influential papers in the flagship journal. In 2012, a paper by Jenerette and Shen addressed the issue of experimentation in landscape ecology in detail. Jenerette and Shen (2012) developed a taxonomy of experiment types (reproduced in this book as Table 3.1), but the focus of that paper was not on explaining how to do such experiments. My goal with this book has been to fill that gap. I have tried to show how it is possible to conduct many of the experiment types outlined by Jenerette and Shen (2012), and implement them at spatial extents ranging from multiple hectares or square kilometres (Chaps. 6 and 7) to very small extents (Chaps. 8 and 9). Large-scale manipulative experiments—such as those discussed in Chap. 6 (e.g., the Stability of Altered Forest Ecosystems (SAFE; Ewers et  al., 2011) or the Biological Dynamics of Forest Fragmentation Project (BDFFP; Bierregaard et al., 1992) —and experimental model landscapes—such as those discussed in Chap. 7 (e.g., the University of Kansas (Holt et al., 1995) or Bowling Green (With & Pavuk, 2011) field experiments) —exemplify experiments at what we typically think of as ‘landscape’ scales. These systems have taught us a great deal about the impacts of habitat loss, fragmentation and connectivity, and have generally been motivated to test hypotheses germane to landscape ecology concepts. At these extents, the most challenging part of experimental design is adequate replication. Other challenges are the time, effort and cost of setting up and maintaining these large experimental systems, as well as ethical issues when clearing land, and logistical issues of minimizing interference from external disturbances (intentional or stochastic). However, they have the advantage of being highly realistic, and often link directly to land

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management challenges and issues. For example, understanding the impact of forest harvest patterns on songbirds (e.g., Schmiegelow et al., 1997; Leston et al., 2018) can inform forest management planning to maximize economic benefit while minimizing negative ecological impacts. Experiments at smaller extents such as mesocosms and microcosms often focus on research questions in community or ecosystem ecology, yet, as we saw in Chaps. 8 and 9, they can be adapted to address landscape ecology questions. For example, placement of mesocosms can be explicitly spatial to test hypotheses about the effects of contagion (e.g., Resetarits & Silberbush, 2016; Pintar & Resetarits, 2017). Mesocosms in particular are amenable to addressing questions about patch quality, and for carrying out perception and tracer experiments to help with identification of landscape structure. Research can also easily use them for in situ and translocation experiments that help deduce how spatial process varies within landscapes. Microcosms, while similar in many ways to mesocosms, allow for slightly different types of experiments. Both are “container” experiments, but the natural containers in microcosms makes it easier do experiments on patch connectivity, for example, by scaling down experimental fragmentation that we saw in Chap. 6 to the extent of moss patches on rocks (e.g., Gilbert et al., 1998), or insects on patches of cacti (e.g., Fletcher et al., 2018). Advantages of small-scale mesocosm and microcosm experiments are potential for low cost and high replication, as well as a great deal of experimenter control over the variables. This may come at a cost of realism, or with realism limited to the small-extent system under study, with challenges in “scaling up” findings from container experiments to larger-scale systems. Ecologists often think about doing experiments as something done “in the field” or with living organisms in a lab or greenhouse. In Chap. 10, I illustrated some of the most common in silico approaches used by landscape ecologists: statistical, mathematical, cellular automata and agent-based models. These can be applied to nearly all of the experiment types outlined by Jenerette and Shen (2012). In silico experiments are really only limited by the skill (and imagination) of the coder, and the computing power of their machine—both of which are surmountable challenges. One of the take-home messages of this book is that experimental design takes careful thought, hard work, and a certain degree of creativity. This creativity also extends to the medium in which we work, and in the penultimate chapter, I encouraged researchers to see opportunities for experiments in environments that may not match our perception of a ‘landscape’. These include seascapes, riverscapes, soundscapes, micro-landscapes and the landscapes of cells and tissues within our own bodies. While these environments may be foreign to some of us, collaboration with marine biologists, acoustic ecologists or medical researchers may help bridge the gap and have mutual benefit. Cancer researchers have articulated the value of taking a landscape ecology approach to cancer (Lloyd et al., 2015) and collaboration with biomedical researchers might also lead to new tools and techniques to address landscape ecology questions.

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12.3  Conclusion The many examples of experiments presented in this book might suggest that I was not fully correct in my claims in the introduction that it is difficult to experiment in landscape ecology. In fact, experimentation in landscapes is very possible. Indeed, in writing this book, it has been exciting and inspiring to see the many creative ways that researchers have done experiments that —in one approach or another—assess whether and how “space matters”. However, to this point in time, we have not had an explicit guide to doing experiments in landscape ecology. I hope that collectively, this book, and the examples therein can help to advance a more experimental approach to landscape ecology. As an initial volume on the topic, I do not think it is the final word. Consistent with the epigraph to this chapter, a good experiment does not lead to definitive answers; it leads to more (and different, and often better) experiments. It is my hope that the cumulative suite of examples, guidance and resources presented in this book lead to more, different and better experiments in landscape ecology.

References Betts, M. G., Hadley, A. S., Frey, D. W., et al. (2021). When are hypotheses useful in ecology and evolution? Ecology and Evolution, 1–15. https://doi.org/10.1002/ece3.7365 Bierregaard, R. O., Lovejoy, T. E., Kapos, V., & Hutchings, R. W. (1992). The biological dynamics of tropical rainforest fragments. BioScience, 42, 859–866. https://doi.org/10.2307/1312085 Diamond, J. (2001). Ecology: Dammed experiments! Science, 294, 1847–1848. https://doi. org/10.1126/science.1067012 Diamond, J. M. (1983). Ecology: Laboratory, field and natural experiments. Nature, 304, 586–587. https://doi.org/10.1038/304586a0 Ewers, R. M., Didham, R. K., Fahrig, L., et al. (2011). A large-scale forest fragmentation experiment: The stability of altered forest ecosystems project. Philosophical Transactions of the Royal Society B Biological Sciences, 366, 3292–3302. https://doi.org/10.1098/rstb.2011.0049 Fletcher, R. J., Reichert, B. E., & Holmes, K. (2018). The negative effects of habitat fragmentation operate at the scale of dispersal. Ecology, 99, 2176–2186. https://doi.org/10.1002/ecy.2467 Gilbert, F., Gonzalez, A., & Evans-Freke, I. (1998). Corridors maintain species richness in the fragmented landscapes of a microecosystem. Proceedings of the Royal Society B: Biological Sciences, 265, 577–582. https://doi.org/10.1098/rspb.1998.0333 Guidetti, P., Parravicini, V., Morri, C., & Bianchi, C. N. (2014). Against nature? Why ecologists should not diverge from natural history. Vie Milieu, 64, 1–8. Hairston, N. G., Sr. (1989). Ecological experiments: Purpose, design, and execution. Cambridge University Press. Holt, R. D., Robinson, G. R., & Gaines, M. S. (1995). Vegetation dynamics in an experimentally fragmented landscape. Ecology, 76, 1610–1624. https://doi.org/10.2307/1938162 Jenerette, G.  D., & Shen, W. (2012). Experimental landscape ecology. Landscape Ecology, 27, 1237–1248. https://doi.org/10.1007/s10980-­012-­9797-­1 Kimmerer, R. W. (2013). Braiding sweetgrass: Indigenous wisdom, scientific knowledge, and the teachings of plants. Milkweed Editions. Kohler, R.  E. (2002). Labscapes and landscapes: Exploring the lab-field border in biology. University of Chicago Presss.

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Leston, L., Bayne, E. M., & Schmiegelow, F. K. A. (2018). Long-term changes in boreal forest occupancy within regenerating harvest units. Forest Ecology and Management, 421, 40–53. Lloyd, M. C., Rejniak, K. A., Brown, J. S., et al. (2015). Pathology to enhance precision medicine in oncology: Lessons from landscape ecology. Advances in Anatomic Pathology, 22, 267–272. https://doi.org/10.1097/PAP.0000000000000078 Pintar, M.  R., & Resetarits, W.  J. (2017). Context-dependent colonization dynamics: Regional reward contagion drives local compression in aquatic beetles. The Journal of Animal Ecology, 86, 1124–1135. https://doi.org/10.1111/1365-­2656.12697 Resetarits, W.  J., & Silberbush, A. (2016). Local contagion and regional compression: Habitat selection drives spatially explicit, multi-scale dynamics of colonization in experimental metacommunities. Ecology Letters, 19, 191–200. Schmiegelow, F. K. A., Machtans, C. S., & Hannnon, S. J. (1997). Are boreal birds resilient to forest fragmentation? An experimental study of short-term community responses. Ecology, 78, 1914–1932. https://doi.org/10.1890/0012-­9658(1997)078[1914:ABBRTF]2.0.CO;2 Underwood, A. J. (2009). Components of design in ecological field experiments. Annales Zoologici Fennici, 46, 93–111. https://doi.org/10.5735/086.046.0203 Varley, G.  C. (1957). Ecology as an experimental science. The Journal of Animal Ecology, 26, 251–261. With, K. A., & Pavuk, D. M. (2011). Habitat area trumps fragmentation effects on arthropods in an experimental landscape system. Landscape Ecology, 26, 1035–1048. https://doi.org/10.1007/ s10980-­011-­9627-­x

Resources

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Chapter 1: Introduction Key Textbooks on Landscape Ecology Farina A (2006) Principles and methods in landscape ecology: towards a science of landscape. Springer, Dordrecht. 412 pp. • This book provides an overview of the key concepts in landscape ecology, including a description of what is a landscape, key theories, as well as a comprehensive discussion of the topics of scale, patterns, processes and dynamics. It also includes chapters on methods and management/conservation issues as well as a glossary. Each chapter also includes suggested readings. The book is written from a European perspective of landscape ecology. Wiens JA, Moss MR, Turner MG, Mladenoff DJ (eds) (2007) Foundation Papers in Landscape Ecology. Columbia University Press, New York. 582 pp. • This is an edited collection of seminal papers in the discipline edited by four members of the first generation of North American landscape ecologists. This is a good volume for anyone wanting to understand the historical and philosophical underpinnings of the discipline as well as trace the early developments of the field. It includes reprints of papers from 1915 to 1990, including several in translation from German/Russian that might otherwise be inaccessible to many readers. The editors include a short introduction and review chapter with each thematic grouping. This is an excellent text for PhD students working towards their comprehensive exam.

 All URLs correct as of March, 2022.

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Turner MG, Gardner RH (2015) Landscape ecology in theory and practice: pattern and process. Springer, New York. 482 pp. • As with the Farina (2006) text, this book is an introductory text that covers the main concepts in the discipline, however this book is from a North American perspective. This is the second edition, and covers topics of scale, metrics, spatial statistics, pattern/process and disturbance. Gergel and Turner (2017) complements this text, and is a useful source for lab exercises in a course. Gergel SE, Turner MG (eds) (2017) Learning Landscape Ecology: a practical guide to concepts and techniques. Springer-Verlag, New York • This book complements Turner et al. (2015) and functions as a lab manual to accompany the textbook. There are a range of exercises that illustrate key concepts, which are aimed a mix of undergraduate and graduate-level skill sets. Each chapter includes background information and the necessary code (using widely available software, such as R) and resources  to teach hands­on skills. With KA (2019) Essentials of Landscape Ecology. Oxford University Press, Oxford. 641 pp. • This is a new textbook for landscape ecology, aimed at a senior undergraduate level, including discussion questions and summary points in each chapter. It is richly illustrated (in colour), and includes an extensive glossary. In addition to covering the key foundational topics, it includes chapters on landscape epidemiology, landscape genetics and chapters on the interface between population, community and landscape ecology. Francis RA, Millington JDA, Perry GLW, Minor ES (eds) (2021) The Routledge handbook of landscape ecology. Routledge, Milton Park. 544 pp. • This is book is part of Routledge’s “Handbook of…” series and is intended as a reference guide to support research and teaching. The chapters are organized in four parts: theory and concepts; landscape processes; methods and tools; and landscape ecology frontiers. Each chapter is written by subject experts; the section on methods and tools complements this text well. Online Resources The International Association of Landscape Ecology (https://www.landscape-­ ecology.org/) or IALE (pronounced “Eye-alley”) is the global organization for the discipline of landscape ecology. Also known colloquially as “IALE World”, the organization exists mainly to support regional chapters while also providing a forum for working groups, communication and resources. The organization hosts a World Congress every four years. You can find the current list of active working groups on the webpage, and join one at no cost. You can also find links to the different regional

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and national-level chapters. Membership in any one regional/national chapter automatically includes membership in IALE. Regional/national chapters generally offer an annual conference, as well as resources like newsletters, LISTSERVs, job boards and mentoring opportunities. Texts on Doing Ecological Experiments in General Hairston Sr. NG (1989) Ecological experiments: purpose, design, and execution. Cambridge University Press, Cambridge. 370 pp. • Though dated, what I appreciate about this book is the first three chapters that provide both some philosophical context for experimentation in ecology, as well as practical advice about the trade-offs and minimum requirements for doing ecology well. The remaining chapters describe experiments in different environments (e.g., forests, marine, freshwater, arid), using examples from the literature. Krebs CJ (1989) Ecological methodology. Harper-Collins, New York. 654 pp. • This classic text in ecology methods focuses mainly on field techniques and the accompanying analytical work (e.g., calculating population size using mark-recapture). Most of the methods described apply to population and community ecology. There is an extensive section on sampling and experimental design that is useful to landscape ecologists; however, the appendices with extensive code are too dated to be useful (although interesting to look at as an historical artifact for those interested in in silico work!). Resetarits Jr. WJ, Bernardo J (eds.) (1998). Experimental ecology: issues and perspectives. Oxford University Press, Oxford. 470 pp. • Although also a bit dated, this book provides examples of ecological experiments in different environments (rivers, coral reefs, deserts) as well as discussion of experiments in mesocosms and with model systems like the Ecotron facility. Miao S, Carstenn S, Nungesser M (eds) (2009) Real Wold Ecology: large-scale and long-term case studies and methods. Springer, New York • This edited collection provides examples of research at large scales and over the long-term. Although not explicitly about landscape ecology experiments, many of the chapters provide practical advice on issues such as spatial controls, spatial statistics, and scale issues. Several of the chapters provide technical content not included in other texts (e.g., structural equation modelling, mass-balance analysis). Karban R, Huntzinger M, Pearse IS (2014) How to do ecology: a concise handbook. 2nd edition. Princeton University Press, Princeton. 182 pp. • This short, easy-to-read book would complement an introductory undergraduate ecology course well. It provides some great discussion on the challenge

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that many students face—which is picking a question and developing hypotheses and experimental design. There is a fair bit of dense information packed in here, but the presentation is light and feels like a conversation with a friendly prof. There are also chapters with practical advice on giving a talk, preparing an article or poster and prepare for a job or grant application. Much of the advice here is simple things that veteran academics might do intuitively but which is good for students and early career professionals to hear specifically.

Chapter 2: Experiments Equity Diversity and Inclusion (EDI) Issues This topic is rightly becoming more prominent in science and ecology. Many societies (e.g., IALE-North America, Ecological Society of America) have recently struck committees to grapple with EDI (sometimes referred to as DEI) issues, and are working to find ways to make the discipline more welcoming to under-represented groups. You can read the IALE-NA statement here: https://www.ialena.org/ uploads/9/4/8/2/94821076/ialena-­final_statement_of_diversity_equity_and_ inclusion.pdf The Ecological Society of America has published a website devoted to the topic, with an extensive list of relevant resources (https://www.esa.org/about/diversity-­in-­ ecology/deij-­resources/). Other suggested readings on this topic include: Demery A-JC, Pipkin MA (2021). Safe fieldwork strategies for at-risk individuals, their supervisors, and institutions. Nature Ecology & Evolution 5, 5–9. Kimmer, RW (2013) Braiding sweetgrass: Indigenous wisdom, scientific knowledge and the teachings of plants. Milkweed Editions, Minneapolis. 410 pp. National Academies of Sciences, Engineering, and Medicine. 2020. The impacts of racism and bias on black people pursuing careers in science, engineering, and medicine: proceedings of a workshop. Washington, DC: The National Academies Press. https://doi.org/10.17226/25849. Philosophy of Science When PhD students are seeking to brush up their “history and philosophy of science” knowledge in advance of their comprehensive exam, these are the texts I recommend. Kohler RE (2002) Labscapes and landscapes: exploring the lab-field border in biology. University of Chicago Press, Chicago and London. 326 pp.

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• Like all historians, Kohler knows how to tell a good story. This book tells the story of the development of field biology in the United States, tracing the development of field work from the late 1900s to the 1950s when the ­discipline of ecology began to be more formalized. This is a nice book have as bedside reading, or to accompany you on a commute. Gauch HGJ (2003) Scientific Method in Practice. Cambridge University Press, Cambridge. 433 pp. • This book broadly  covers how we do science. While dense (definitely not bedside reading!), it is well-written, and includes a concise history of science and a clear overview of the philosphy of science, including presuppositions, logic, probability and parsiomny. Examples come from across science. The decription of Bayesian approaches (Chaps. 6 and 7) is the clearest introduction to Bayesian statistics I have ever encounterd. Beisner BE, Cuddington K (eds) (2005) Ecological Paradigms Lost: Routes of Theory Change, Academic Press. 588 pp. • This book traces how ideas have devleoped within ecology. The format includes two chapters providing historical overview and opinion on each topic (e.g., population, community, ecosystem ecology); one by a younger ecologist and one by a more established one, followed by a chapter by a philosopher of science. While the entire volume is very readable, graduate students could elect to focus on the section that matches their subdiscipline. Unforuntately there is no section on landscape ecology; perhaps a future edition will include one. Betts MG, Hadley AS, Frey DW, et al (2021) When are hypotheses useful in ecology and evolution? Ecology and Evolution 11, 5762–5776. https://doi. org/10.1002/ece3.7365 • This article is a concise summary of many of the complex ideas is the above books. You should not read it as a substitute for the larger discourses, but rather as a supplement! It nicely summarizes the principle of falsification, hypothesis generation, and key challenges in ecological field experimental design. Kimmel K, Dee LE, Avolio ML, Ferraro PJ (2021) Causal assumptions and causal inference in ecological experiments. Trends in  Ecology and Evolution, 36, 1141–1152. https://doi.org/10.1016/j.tree.2021.08.008 • This article outlines how inferring causality in ecological experiments can be tricky if we do not consider assumptions carefully. The paper outlines four key assumptions (excludability, no interference, no multiple versions of treatments and no noncompliance) and offers clear examples and suggested remedies.

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Chapter 3: Landscape Ecology Experiments Space-for-Time Studies Space in the book did not allow for an in-depth discussion of Long-Term Ecological Research Sites (LTERs). These are fantastic locations to do ecological research, of any kind, including landscape ecology experiments. In the United States, the LTER Network (https://lternet.edu/) provides a centralized source of information on 28 LTER sites across the country, as well as synthesizing data, findings, methods and other resources. Other countries have LTER sites and networks (e.g., LTER-D in Germany) – Google “LTER” and a country name to see if there is one near you! Quasi-Experiments Butsic V, Lewis DJ, Radeloff VC, et al (2017) Quasi-experimental methods enable stronger inferences from observational data in ecology. Basic and Applied Ecology 19, 1–10. https://doi.org/10.1016/j.baae.2017.01.005 • This paper gives a tutorial on quasi-experimental statistical analyses (based on statistics from economics, but adapted for ecology). The supplemental files include sample data and code to carry out the different types of analyses demonstrated in the paper (matching, regression discontinuity, difference-in-difference modelling, and instrumental variables) using both R and STATA software.

Chapter 4: Pseudoreplication  xperimental Design (or Strategies to Help You Avoid E Accusations of Pseudoreplication) The following are highly recommended to help you with robust experimental design and development of EMS models, as well as making decisions about fixed vs. random effects: Quinn GP, Keough MJ (2002) Experimental design and data analysis for biologists. Cambridge University Press, Cambridge Eberhardt LL, Thomas JM (1991) Designing environmental field studies. Ecol Monogr 61:53–73. https://doi.org/10.2307/1942999 Wilk MB, Kempthorne O (1955) Fixed, Mixed, and Random Models. J Am Stat Assoc 50: 1144–1167 Be sure to consult Table 1 in the Open Access paper below:

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Davies GM, Gray A (2015) Don’t let spurious accusations of pseudoreplication limit our ability to learn from natural experiments (and other messy kinds of ecological monitoring). Ecology and Evolution 5, 5295–5304. https://doi. org/10.1002/ece3.1782 • To see some of the information in the above references presented online in course format with video demonstrations, check out the Open Educator unit on “Design of Experiments”: https://www.theopeneducator.com/doe Meta-analysis Koricheva J, Gurevitch J, Mengersen K (eds) (2013) Handbook of meta-analysis in ecology and evolution. Princeton University Press, Princeton, NJ • A highly recommended text for embarking on meta-analysis. O’Dea RE, Lagisz M, Jennions MD, et al (2021) Preferred reporting items for systematic reviews and meta-analyses in ecology and evolutionary biology  : a PRISMA extension. https://doi.org/10.1111/brv.12721 • This paperguides  you through how to document your work properly  when doing a systemic review or meta-analysis to meet standards of reproducability. PLOS also has a number of blog postings on the topic of meta-analysis, see www. absolutely.maybe.plos.org and search for “meta-analysis” Sampling Issues Williams BK, Brown ED (2019) Sampling and analysis frameworks for inference in ecology. Methods in Ecology and Evolution 10, 1832–1842 • This paper discusses how sampling design affects inference. It compares design-based and model-based inference frameworks with a focus on survey data. Statistical Analysis If you feel you never grasped statistics when you first took it, or your last stats course is a hazy memory, I recommend these two texts as an easy-to-digest entry to statistics  – they are ideally presented for those who feel like they are not “math people”. Fowler J, Cohen L, Jarvis P (1998) Practical statistics for field biology. 2nd edition. John Wiley Sons, Chichester, UK. 259 pp.

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van Emden H (2008) Statistics for terrified biologists. Blackwell Publishing, Malden MA. 343 pp. As well, spatial statistics are a special group of statistics particularly relevant to landscape ecologists. These volumes are highly recommended. Dale MRT, Fortin M-J (2021) Quantitative analysis of ecological networks. Cambridge University Press, Cambridge. 300 pp. Dale MRT, Fortin M-J (2014) Spatial analysis. A guide for ecologists. 2nd edition. Cambridge University Press, Cambridge. 454 pp. Fletcher R, Fortin M-J (2019) Spatial ecology and conservation modeling: applications with R. Springer, NY. 487 pp.

Chapter 5: Scale Here are some classic readings on scale, which are relevant to grappling with the concept in a landscape ecology context. Papers O’Neill R V, Johnson AR, King AW (1989) A hierarchical framework for the analysis of scale. Landscape Ecology, 3,  193–205. https://doi.org/10.1007/ BF00131538. Turner MG, O’Neill R V., Gardner RH, Milne BT (1989) Effects of changing spatial scale on the analysis of landscape pattern. Landscape Ecology, 3,153–162. https://doi. org/10.1007/BF00131534 Turner MG, O’Neill R V., Gardner RH, Milne BT (1989) Effects of changing spatial scale on the analysis of landscape pattern. Landscape Ecology, 3,153–162. https://doi.org/10.1007/BF00131534 Urban DL, O’Neill RV, Shugart HH (1987) Landscape ecology: a hierarchical perspective can help scientists understand spatial patterns. Landscape Ecology 37,119–127 Wiens JA (1989) Spatial Scaling in Ecology. Functional Ecology 3,  385–397. https://doi.org/10.2307/2389612 Books Ehleringer JR, CB Field (eds.) (1993) Scaling physiological processes: leaf to globe. Academic Press, San Diego CA. 388 pp. Peterson DL, VT Parker (eds.) (1998) Ecological scale: theory and applications. Columbia University Press, NY. 608 pp.

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Richie ME (2009) Scale, heterogeneity, and the structure and diversity of ecological communities. Princeton University Press, NJ. 240 pp. Schneider, DC (2009) Quantitative ecology: spatial and temporal scaling, 2nd edition, Academic Press. Whyte LL, AG Wilson, D Wilson (eds.) (1969) Hierarchical Structures. Elsevier, NY. 334 pp.

Chapter 6: Large-Scale Manipulations If you think you would like to experiment using large-scale manipulations then working on one of the existing projects listed below is a good strategy. The websites will give you project background, a list of projects and publications that have arisen from each project, as well as details about how you can become involve. Listings of URLs are up-to-date as of March 2022. Project Websites Biological Dynamics of Forest Fragments (BDFFP): https://forestgeo.si.edu/ research-­p rograms/affiliated-­p rograms/biological-­d ynamics-­f orestfragments-­project-­bdffp Calling Lake Experiment: https://healthylandscapesebm.ca/casestudy/ calling-­lake-­fragmentation-­study/ Extreme Drought in the Grasslands Experiment (EDGE): https://www.usgs.gov/ centers/southwest-­b iological-­s cience-­c enter/science/colorado-­p lateau-­ extreme-­drought-­grassland Global Treeline Range Expansion Experiment (G-TREE): http://treelineresearch.com/ Inner Mongolia Grassland Experiment: http://leml.asu.edu/IMGRE/ International Institute for Sustainable Development (IISD) Experimental Lakes Area: https://www.iisd.org/ela/ Konza Prairie: http://www.konza.ksu.edu/Splash/default.aspx Missouri Ozark Forest Ecosystem Project (MOFEP): https://mdc12.mdc.mo.gov/ applications/MOFEP/index.html Stability of Altered Forest Ecosystems (SAFE) project: https://www.safeproject.net/ Teakettle Experiment: http://www.hurteaulab.org/teakettle-­experiment.html

Chapter 7:Experimental Model Landscapes As with the large-scale experiments in Chap. 6, some of the projects described in Chap. 7 arelong-running and (as of 2022) are ongoing. Consult the websites for more information.

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Jena Experiment: http://the-­jena-­experiment.de/ Miami University Ecology Research Center: http://miamioh.edu/cas/academics/ centers/erc/ University of Kansas Field Station: https://biosurvey.ku.edu/field-­station Although related only to fragmentation experiments in forested landscapes, the BIOFRAG database, as described in the Open Access paper below, provides access to data and metadata on a number of experiments described in Chaps. 6 and 7, as well as other observational studies. Pfeifer M et  al. (2014) BIOFRAG  – a new database for analyzing BIOdiversity responses to forest FRAGmentation. Ecology and Evoluation 4, 1524–1537.

Chapter 8: Mesocosm Resources Byers RJ, Odum HT (1993) Ecological Microcosms. Springer-Verlag, NY. 557 pp. • Although the title is “microcosms”, this text is a comprehensive overview of mesocosm studies. There is practical information for setting up terraria, aquaria and other types of container experiments, with examples from the literature. Roy J, Rineau F, De Boeck HJ, et al (2021) Ecotrons: powerful and versatile ecosystem analysers for ecology, agronomy and environmental science. Global Change Biology 27, 1387–1407 • This paper provides an overview of 13 ecotrons (some of which were still under construction at the time of writing) around the world, and discusses in detail, the features that enable novel research in ecotron facilities. The Metatron: https://themetatron.weebly.com/ • The metatron contains 48 cages, which are each 100  m2 and connected by corridors, facilitating experiments in fragmentation/connectivity. The microclimate of each cage can be controlled to allow experiments on patch conditions. The Ecotron: http://the-­jena-­experiment.de/index.php/ecotron/ • The Jena experiment described in Chap. 7 also contains an ecotron facility. The ecotron contains 24 units, which can contain one to four isolated ecosystems.

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Chapter 10: In Silico Experiments Information About Software and Models Described in Chap. 10. LANDIS-II: http://www.landis-­ii.org/ • This website is where you can download the LANDIS-II software, and access examples of projects, publications, as well as information about training and conferences. If you are interested in implementing LANDIS-II, see the paper below for a step-by-step guide. Suárez-Muñoz M, Mina M, Salazar PC, et al (2021) A step-by-step guide to initialize and calibrate landscape models: a case study in the Mediterranean mountains. Frontiers in Ecology and Evolution 9, 209 R and Rstudio: https://cran.r-­project.org/ Hesselbarth MHK, Nowosad J, Signer J, Graham LJ (2021) Open-source tools in R for landscape ecology. Current Landscape Ecology Reports 6, 97–111 • This paper provides an overview of the most recent R packages relevant to landscape ecology, with tips for beginning and advanced R users. Phillps ND (2018) YaRrr! The Pirate’s Guide to R. https://bookdown.org/ndphillips/YaRrr/ • This online, Open Access book is my favourite, user-friendly introduction to using R. I frequently share it with undergraduates and colleagues making the leap to using R. If you have never used R, but want to, I highly recommend starting here. FUTURES: https://cnr.ncsu.edu/geospatial/research/futures/ • This website provides a place to learn more about the open source urban growth model FUTURES (FUTure Urban-Regional Environmental Simulation). The site gives links to tutorials and an online manual, as well as an online forum and recent publications. WoodPaM model: https://blogs.epfl.ch/francois.gillet/ • This site has a short description of the model, which uses mathematical models to develop scenarios for patches in a silvipastoral landscape. Model components include tree recruitment, and interactions between wood, herbs, and cattle grazing. DYPAL: http://amap-­collaboratif.cirad.fr/pages-­logiciels/?page_id=70 • The DYnamic PAtchy Landscapes model is a simulation model for landscape management. This site has a link to download the software and a short bibliography.

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MAIDEN: https://figshare.com/articles/code/MAIDEN_ecophysiological_forest_ model/5446435 • The Modelling and Analysis IN DENdrochonology tool is an ecophysiological model written in C++ System Dynamic Models: https://vensim.com/ • The urban landscape papers that used SD models carried out programming on the Vensim platform, a proprietary software. For guidance on SD models in R, see Duggan J (2016) System Dynamics Modeling with R.  Springer International Publishing. Switzerland. Resources to Increase Reproducibility FigShare (https://figshare.com/), Dryad (https://datadryad.org/stash), • FigShare and Dryad are repositories for data, and promote Open Science. Many journals require you to publish data on one of these sites. The advantage of depositing data in one of these sites is that data are citable. There are slight differences between the two, and individuals have their preference of which to use. Dryad is non-profit and community-led and uses curators to check files and help you follow best practices. Zenodo (https://zenodo.org/) • Zenodo is a data deposit (like FigShare and Dryad) and also allows research to deposit papers, software code and reports. It provides a “sandbox” environment (http://sandbox.zenodo.org) for developers to test API integration. GitHub (https://github.com/) • GitHub is a platform for software development. It allows you to publish code for others to use. It is extremely useful for collaborative work, and includes version control. ODD protocol • The Overview, Design concepts and Details (ODD) protocol helps standardize the publicized descriptions of models, specifically agent-based models. Anyone publishing a paper with an agent-based model should use this model. Guidelines are described in the papers below. Grimm V et  al. (2020) The ODD protocol for describing agent-based and other simulation models: a second update to improve clarity, replication, and structural realism. Journal of Artificial Societies and Social Simulation 23: 7. Available online http://jasss.soc.surrey.ac.uk/23/2/7.html Grimm, V, Berger U, DeAngelis DL, Polhill JG, Giske J, Railsback SF (2010) The ODD protoecol: a review and first update. Ecological Modelling 221: 2760–2768

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Grimm, V. et  al. (2006) A standard protocol for describing individual-based and agent-based models. Ecological Modelling 198: 115–126. Society for Open, Reliable, and Transparent Ecology and Evolutionary Biology (SORTEE): www.sortee.org • This society promotes increased reliability and transparency in the ecological science and related fields. Anyone is welcome to join. The webpage has information about conferences, and an extensive resources page (including links to courses, online materials and readings) Cloud Computing If your desktop computer or local cluster does not give you the computing power you need, and you do not have the resources to develop your own server network, cloud computing can be a good resource. These give you access to virtual machines and a higher amount of memory/core than you might otherwise have. Examples include Amazon Web Services Elastic Compute Cloud (known as AWS EC2) (https://aws.amazon.com/ec2/), Digital Ocean (https://www.digitalocean.com/), Microsoft Azure (https://azure.microsoft.com/en-­us/) and Google Compute Engine (https://cloud.google.com/compute).

Chapter 11: Novel Landscapes Seascapes Pittman SJ (ed. . (2018) Seascape Ecology. Wiley Blackwell, Hoboken, NJ. 526 pp. • A comprehensive text that aims to help researchers across disciplines (marine bioogy, environmental science, coastal management) undertand how bringing a landscape ecology perspective to the marine environment. The book introduces seascape ecologist concepts (which will be familiar to landscape ecologists) like patches, scale, and connectivity, but describes their applicatoin in a marine context. It also covers topics specific to the marine realm, including mapping issues and the ecological and management of different marine habitats (e.g., salt-marsh, seagrass). Soundscapes Farina A (2014) Soundscape Ecology: Principles, patterns, methods and applications. Springer, Dordrecht. 315 pp.

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• This is written as a handbook for a graduate course in landscape ecology, with a focus on how “soundscapes” integrate methods and concepts from bioacoustics, acousitc ecolgy and behavoural ecology. It introduces principles, theories, methods and applications. Some other useful methods papers include the following: McKenna MF, Shannon G, Fristrup K (2016) Characterizing anthropogenic noise to improve understanding and management of impacts to wildlife. Endangered Species Research 31, 279–291. https://doi.org/10.3354/esr00760 Merchant ND, Fristrup KM, Johnson MP, et al (2015) Measuring acoustic habitats. Methods in Ecology and Evolution 6,  257–265. https://doi.org/10.1111/ 2041-210X.12330 Shannon G, McKenna MF, Angeloni LM, et al (2016) A synthesis of two decades of research documenting the effects of noise on wildlife. Biological Reviews 91, 982–1005. https://doi.org/10.1111/brv.12207 Pumilio (http://ljvillanueva.github.io/pumilio/) • Pulimo is a Soundscape Information Systems. Pulimo is no longer maintained, but is available on GitHub for others to expand on. Pulimo is designed for management and visualization of sound files. Kaleidoscope (https://www.wildlifeacoustics.com/products/kaleidoscope-­pro) • This is commercial software that allows you to sort, label and identify audio recordings of bird songs.

Glossary

Adaptive management (Chap. 6)  sometimes characterized as ‘learning while doing’. Active adaptive management matches the use of this term in Chap. 6. In active adaptive management, data at a given point in time are used to specify a range of alternative management strategies, which are articulated as testable hypotheses. Management is then applied in an experimental fashion (Walters and Holling 1990). Aspatial (Chaps. 1 and 10)  not related to, or not associated with a particular space or area. Control (Chaps. 2 and 3)  a set of observations that are identical to those to which an experiment is being applied, except in the factor of interest. Evaluation unit (Chap. 2)  Equivalent to sampling unit. See sampling unit entry. Experimental unit (Chap. 2)  the smallest division of the experimental material such that any two units may receive different treatments (or treatment combinations) in a manipulative experiment or have different ecological conditions for a mensurative experiment” (Krebs 1989). Extent (Chaps. 1 and 5)  The overall area encompassed by the study (Wiens 1989); the largest scale of heterogeneity to which an organism responds (from Kotliar and Wines 1990). Fixed effect (Chap. 4)  There are several different ways in which fixed effects are defined/characterized. One is that they are the factors that are of interest to the researcher, and are the things we measure in the field as independent variables or manipulate in the experiment (Quinn and Keough 2002). Eisenhart (1947) suggests that the researchers ask themselves if the conclusions apply to what is actually under study, or whether they are to be generalized to a larger as a means to distinguish fixed vs. random effects. Lawson (2015: 142) described a fixed effect (he uses the term “fixed factor”) as “when the purpose of the experimentation is to study differences in the average response caused by differences in factor levels, the factors in the experiment are called fixed”. Thus, depending

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on the purpose of the experiment, a given variable may be designated as a fixed effect in one case, but a random effect in another. See also definition below for random effect. Fractal dimension (Chap. 5)  is a measure of the statistical complexity in a geometric shape. The index D is a non-integer that measures between 1 and 2 and allows for a comparison of how the details of a geometric pattern chance with the scale at which the pattern is measured. For example, the length of a coastline of a given geographic feature increases as the scale of the measuring unit decreases (from Mandelbrot 1983). Grain (Chap. 5)  The size of the individual units of observation (Wiens 1989); the smallest scale at which an organism responds to the pattern of patches on the landscape (i.e., to patch structure; from Kotliar and Wiens 1990). Hierarchical structure (Chaps. 1 and 5)  Describes how a biological system is composed of interacting components (i.e., lower-level entities) and is itself a component of a larger system (i.e., higher-level entities) (from O’Neill et al. 1989). Hypothetico-deductive approach (Chap. 2)  a component of the scientific method whereby hypotheses are developed based on theory and are used to predict future events under different conditions. These are examined against empirical data to verify or falsify the hypothesis. Interdisciplinary (Chaps. 1 and 3)  research that involves several unrelated academic disciplines working towards a common research goal; boundary-­crossing across subject areas is necessary to develop integrative research and create new knowledge (Tress et al. 2005). Landscape (Chaps. 1 and 5)  an area that is spatial heterogeneous in at least one factor of interest; a spatial mosaic of patches (from Forman and Godron 1981). Lacunarity (Chap. 5)  This term comes from the Latin ‘lacuna’ (holes). Lacunarity is a measure of the spatial pattern in a landscape, with a focus on characterizing the gaps/holes in the spatial pattern. The lacunarity metric is dimensionless and was originally developed as a way to describe fractals (Dale 2000). Mesocosm (Chaps. 8 and 9)  “a contained subset of a larger ecological system, such as an aquarium filled with pond biota” (Srivastava et al. 2004: 379). Meta-analysis (Chap. 4)  an “analysis of analyses”. A statistical synthesis of effect sizes from multiple independent studies (O’Dea et al. 2021). Microcosm (Chaps. 8 and 9)  “a small, contained ecological system” (Srivastava et al. 2004: 379). Examples include tide pool, pitcher plants, tank bromeliads. Non-stationarity (Chap. 5)  Non-stationary processes are those where the means, variance and co-variances change over time – often in unpredictable, stochastic ways. Systems with non-stationarity are difficult to model, and predictions about how the system will behave at a future point in time or in a different location are inaccurate. Patch (Chap. 5)  a defined area which is homogenous in one or more characteristics (e.g., land cover, stand age, soil type) relative to the surrounding area (from Forman and Godron 1981). Patch-mosaic model (Chap. 1)  a framework that describes a landscape whereby its properties arise from the configuration and composition of the individual

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patches (Turner and Gardner 2015; With 2019). The framework is analogous to tile mosaics. One of the most famous mosaics in the world is the on in St. George’s Church in Topola, Spain. As with a landscape, the individual tiles (equivalent to “patches”) have their own unique properties of size, colour, and shape. We could summarize the composition of the mosaic at St. George in terms of the distribution of its millions of tiles across the 15,000 colours, but this data would not do justice to the beauty of the artwork, just as a landscape is more than the simple sum of the parts. Pseudoreplication (Chaps. 2, 3 and 4)  this concept is often misunderstood. It refers to an experimental design that inflates the number of independent samples or replicates, thereby affecting the statistical power. It was first introduced in a widely cited paper by (Hurlbert 1984). Since then ecologists have debated the whether it is as critical a problem as originally stated, with some declaring that pseudoreplication is an inevitable component (a sine qua non) of spatial ecology that needs to be accommodated (Hargrove and Pickering 1992). Debate is ongoing (see Chap. 4). Random effect (Chap. 4)  See also fixed effect. Random effects are those that are a random selection from a larger possible group (Quinn and Keough 2002). Lawson (2015: 142) described a random effect (or random factor) as happening “when the purpose of the experimentation is to study the variance caused by changing levels of a factor”. Sampling unit (Chap. 2)  the unit on which a measurement or response is being made. Sampling units are assumed to be independent from each other, and cannot be further subdivided. Sampling units may be subsets of an experimental unit. Scale (Chaps. 1 and 5)  we can describe the concept of “scale” verbally, graphically, and mathematically. There are different types and measurements of scale (e.g., temporal, cartographic); the definition germane to landscape ecology is that “scale refers to the extent relative to the grain of a variable in time or space (Schneider 2001). Scale of effect (Chap. 5)  the spatial extent at which the measured landscape structure best predicts the response of interest (from Jackson and Fahrig 2015). Scaling rules (Chap. 5)  Also known as scaling laws. An approach in which patch hierarchies are used to simplify the complexity of system under study, enhance ecological understanding, and minimize the danger of intolerable error propagation in translating information across multiple scales (from Wu 1999). Spatial autocorrelation (Chaps. 2, 3 and 4)  the phenomenon whereby things which are closer together in geographic space, are more similar (i.e., more autocorrelated), following from Tobler’s first law of geography. Spatial autocorrelation can confound assumptions of many statistical tests, and can also be usefully leveraged when doing spatial interpolation. It is often visualized via variograms or correlograms, and the degree of spatial autocorrelation can be quantified using Moran’s I (Fortin and Dale 2005; Wagner and Fortin 2005). Spatial composition (Chap. 5)  the variety and abundance of patch types within a landscape (from McGarigal and Marks 1995).

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Glossary

Spatial configuration (Chap. 5)  the physical distribution of spatial character of patches within the landscape (from McGarigal and Marks 1995). Spatially explicit (Chaps. 1, 4 and 10)  a study or model in which space is referenced explicitly to points in geographic space (e.g., models or studies with spatial-referenced maps) (Perry and Enright 2007; DeAngelis and Yurek 2017). Spatially implicit (Chaps. 1, 4 and 10)  a study or model in which space is implied; they do not reference particular geographic locations but may reference space in general terms (e.g., degree of aggregation, distances between components) (Perry and Enright 2007; DeAngelis and Yurek 2017). Statistical power (Chap. 2)  the measure of how likely it is that a test has reached the correct conclusion (i.e., the probability of rejecting the null hypothesis when it is, in fact false). (Fowler et al. 1998). Theory (Chap. 2)  a well-substantiated explanation of a natural phenomenon. A theory can make use of facts, laws and hypothesis. Note that this scientific definition of a theory is opposite to the everyday use of the word, which implies a guess or a wild idea. Transdisciplinary (Chap. 1)  as with interdisciplinary research (see definition), research that involves academics from across unrelated disciplines, but also includes non-academics, all working collaboratively to a common goal. Participatory research involving land managers or user groups is an example of transdisciplinary research (Tress et al. 2005).

Glossary References

Dale, M. R. T. (2000). Lacunarity analysis of spatial pattern: A comparison. Landscape Ecology, 15, 467–478. https://doi.org/10.1023/A:1008176601940 DeAngelis, D. L., & Yurek, S. (2017). Spatially explicit modeling in ecology: A review. Ecosystems, 20, 284–300. https://doi.org/10.1007/s10021-­016-­0066-­z Eisenhart, C. (1947). The assumptions underlying analysis of variance. Biometrics, 3, 1–21. Forman, R. T. T., & Godron, M. (1981). Patches and structural components for a landscape ecology. BioScience, 31, 733–740. https://doi.org/10.2307/1308780 Fortin, M.  J., & Dale, M.  R. T. (2005). Spatial analysis: A guide for ecologists. Cambridge University Press. Fowler, J., Cohen, L., & Jarvis, P. (1998). Practical statistics for field biology (2nd ed.). Wiley. Hargrove, W. W., & Pickering, J. (1992). Pseudoreplication: A sine qua non for regional ecology. Landscape Ecology, 6, 251–258. https://doi.org/10.1007/BF00129703 Hurlbert, S. H. (1984). Pseudoreplication and the design of ecological field experiments. Ecological Monographs, 54, 187–211. Kotliar, N.  B., & Wiens, J.  A. (1990). Multiple scales of patchiness and patch structure: A hierarchical framework for the study of heterogeneity. Oikos, 59, 253–260. https://doi. org/10.2307/3545542 Krebs, C. J. (1989). Ecological methodology. Harper Collins. Lawson, J. (2015). Design and analysis of experiments with R. CRC Press. Mandelbrot, B. B. (1983). The fractal geometry of nature. W.H. Freeman. O’Dea, R. E., Lagisz, M., Jennions, M. D., et al. (2021). Preferred reporting items for systematic reviews and meta-analyses in ecology and evolutionary biology: A PRISMA extension.https:// doi.org/10.1111/brv.12721 O’Neill, R. V., Johnson, A. R., & King, A. W. (1989). A hierarchical framework for the analysis of scale. Landscape Ecology, 3, 193–205. https://doi.org/10.1007/BF00131538 Perry, G. L. W., & Enright, N. J. (2007). Contrasting outcomes of spatially implicit and spatially explicit models of vegetation dynamics in a forest-shrubland mosaic. Ecological Modelling, 207, 327–338. https://doi.org/10.1016/j.ecolmodel.2007.05.010 Quinn, G.  P., & Keough, M.  J. (2002). Experimental design and data analysis for biologists. Cambridge University Press. Srivastava, D. S., Kolasa, J., Bengtsson, J., et al. (2004). Are natural microcosms useful model systems for ecology? Trends in Ecology & Evolution, 19, 379–384. https://doi.org/10.1016/j. tree.2004.04.010

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Glossary References

Tress, G., Tress, B., & Fry, G. (2005). Clarifying integrative research concepts in landscape ecology. Landscape Ecology, 20, 479–493. https://doi.org/10.1007/s10980-­004-­3290-­4 Turner, M. G., & Gardner, R. H. (2015). Lanscape ecology in theory and practice: Pattern and process. Springer. Wagner, H.  H., & Fortin, M.  J. (2005). Spatial analysis of landscapes: Concepts and statistics. Ecology, 86, 1975–1987. https://doi.org/10.1890/04-­0914 Walters, C.  J., & Holling, C.  S. (1990). Large-scale management experiments and learning by doing. Ecology, 71, 2060–2068. Wiens, J.  A. (1989). Spatial scaling in ecology. Functional Ecology, 3, 385–397. https://doi. org/10.2307/2389612 With, K. A. (2019). Essentials of landscape ecology. Oxford University Press. Wu, J. (1999). Hierarchy and scaling: Extrapolating information along a scaling ladder. Canadian Journal of Remote Sensing. https://doi.org/10.1080/07038992.1999.10874736

Index

A Adaptive management, 76, 150, 174 Analysis of Variance (ANOVA), 38, 110 B Before-after-control-impact (BACI), 17, 42, 49, 169, 172 Biological Dynamics of Forest Fragments Project (BDFFP), 78, 80, 85, 86, 101, 191 Block sampling design, 19, 31, 42, 63, 92, 97, 109 Bowling Green Fragmentation Experiment, 73, 91–93, 95, 96, 98, 101, 102, 148, 168, 176, 177, 191 C Calling Lake Fragmentation Study, 77, 78, 85, 99 Cloud computing, 152 Conservation, 5, 6, 60, 85, 100, 102, 164, 173 Conservation biology, 5 D Deductive, 12, 16, 45, 48, 138 Descriptive models, 137 E Ecotron, 109, 110 Equity, diversity, inclusion (EDI), see Ethics

Error, 7, 36, 37, 39, 42, 46, 49, 137 Ethics, 11, 85 Evenstad experiment, 91, 93, 99–100 Expected mean squares (EMS), 38–42, 47 Experimental Lakes Area (ELA), 48, 84, 85 Experiments realism, 30, 32, 51, 60, 61, 74, 76, 95, 118, 124, 139, 192 taxonomy of, 75 trade-offs, 28–30, 43, 51, 60, 61, 85, 107, 109, 137, 144, 162 types of, 20, 23, 29–30, 49 validity of, 28, 136 Experiment type connectivity, 93, 115–117, 129–130, 176 constructed landscape, 176 creation of novel landscapes, 94 distributed, 83 ex situ, 139 fragmentation, 93, 131, 176 in situ, 80, 105, 113 internal patch, 114–115 internal patch manipulation, 80, 82, 100, 128–129, 163, 172, 177 patch shape, 93 perception, 83, 111–112, 126–127, 173 scale manipulation, 177 tracer, 112–113, 127–128, 162 tracer experiment, 81 translocation, 114 translocation experiment, 81 transport manipulation, 81 vector manipulation, 117, 170

© Springer Nature Switzerland AG 2022 Y. F. Wiersma, Experimental Landscape Ecology, Landscape Series 29, https://doi.org/10.1007/978-3-030-95189-4

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216 Extent, 7, 18, 24, 26, 27, 31, 35, 44, 45, 48, 55, 58–60, 64, 65, 73, 74, 76, 78, 81, 83–86, 91, 92, 96, 102, 108, 110, 113, 116, 128, 129, 142, 144, 174, 177, 178, 190, 192 See also Grain Extreme Drought in the Grasslands Experiment (EDGE), 83 F Falsification, 12, 16–17 Fixed effect, 37–40, 42, 45, 50, 110, 168 Fractal, 58, 59, 96, 128 FRAGSTATS, 59, 169 F-ratio, 37–40, 42, 49, 78 FUTURES model, 144 G Geographic information systems (GIS), 5, 20, 24, 50, 135, 136, 138, 142, 148, 150, 173 Global Treeline Range Expansion Experiment (G-TREE), 86 Grain, 55, 58, 59, 62, 64, 65, 112, 127, 175, 176 See also Extent H Hierarchical patch dynamics (HPD) paradigm, 62 Hierarchy theory, 56, 61, 62 History of ecology, 6, 12–16, 19 History of science, 12–16 Hubbard Brook, 17–19, 48, 76, 84 Hypothesis, 13, 16, 20, 24, 26, 35–37, 45–50, 74, 98, 101, 102, 107, 110, 135, 138, 141, 180, 190, 191 I Inductive, 12, 46, 49, 138 Inner Mongolian Grassland Removal Experiment (IMGRE), 82–84 Interdisciplinary, 5, 25, 47, 136, 152, 180

Key concepts, 3 Konza Prairie Biological Station, 82, 83 L LANDIS, 143, 144 Landscape Ecology (journal), 3, 26, 27, 31, 59, 63, 64, 136, 160, 167, 170 Landscapes complexity of, 25 Long-Term Ecological Research (LTER), 64 M Mesocosm advantages, 108 disadvantages, 109 effects, 107 vs. microcosm, 105, 123 Meta-analysis, 27, 45, 47, 60, 86, 101 Metatron, 108, 117 Miami University experiment, 97–98 Models descriptive, 137 mathematical, 143 mechanistic, 137 movement, 145, 146, 148 statistical, 141–143 Model system, 14, 99, 124, 126, 175 N National Ecological Observational Network (NEON), 64 Natural experiment, 15, 16, 19, 45, 46, 49, 73, 82, 109, 145, 165, 171 Natural history, 6, 12, 13, 19, 20, 23–25, 47, 189 O Observational experiment, 13, 14, 18, 23, 26, 30, 31, 35, 38, 39, 50, 59, 61, 117, 142, 162, 163, 167, 169 Observational study, 14–16, 30, 31, 44, 51, 60, 76, 83, 100, 114, 126, 165 ODD protocol, 148, 152 Open-source, 152

J Jena experiment, 91–93, 95, 99, 100, 163 K Kansas Fragmentation experiment, 91, 98 Kansas Habitat Fragmentation experiment, 97

P Pseudoreplication debates about, 43–45 definitions of, 36 solutions for, 46–50

Index R Random effect, 37–40, 42, 50, 110, 142, 167, 168 Randomization, 17, 19, 20, 23, 25, 27, 74, 136, 191 RULE software, 96, 176 S Sampling unit, 18, 50 Savannah River experiment, 73, 78, 80, 81, 101, 129 Scale challenges with, 59–61 taxonomic, 58 temporal, 44, 58, 109, 151 Scaling, 3, 7, 26, 29, 57–59, 61, 63–65, 107, 109, 175, 192 Simulation models, 27, 117, 138, 150 Space-for-time substitution, 14, 25, 30, 39, 45, 47

217 Spatial autocorrelation, 18, 28, 32, 42 Spatial heterogeneity, 4, 64, 83, 165, 178 Spatially explicit, 37 Spatially implicit, 37 Spatial variation, 28, 98, 136 Stability of Altered Forest Ecosystems (SAFE) project, 78, 80, 85, 86, 101, 115, 191 Statistical inference, 19, 36, 139 T Temporal variation, 18 Type I error, 16, 39, 110 Type II error, 16 W Wog Wog Fragmentation Experiment, 78, 101 WoodPaM model, 144, 151