If you’re a very avid reader of this blog, you
need to get a life will know that I’m writing a book about ecology. It’s for University of Chicago Press. The working title is “Ecology At Work”, though that’s only one of several candidate titles. Other candidate titles include “Ecology Master Class”, “Re-engineering Ecology”, and the joke titles that I and others tweeted recently.
Anyway, I’m very excited by this new challenge I’ve set myself, and also very nervous that I can pull it off. Which is where you come in. Below the fold is a draft introduction to my book. Please tear it apart.
Ok, don’t just tear it apart; any and all feedback is most welcome. But critical feedback and suggestions for improvement are particularly welcome. If you think the style sucks, or that the book sounds boring, or whatever, you are not doing me any favors unless you tell me that!
Feel free as well to ask me questions about the book, suggest things I should read, etc.
I’ll of course be getting feedback from more traditional sources as well. But every little helps.
Since many readers prefer not to comment, at the end there’s a little poll for you to tell me what you thought.
UPDATE: The comments have already given me some good feedback: it’s not as clear as it should be up front what the book is about and who the target audience is. And for some readers it’s still not totally clear even by the end. So: the book will comprise comparative case studies of what works and what doesn’t in ecological research. It’s not an introductory ecology textbook, it’s not a methods handbook, and it’s not an “ecology grad student skills” manual like How To Do Ecology. If you think of it as “kind of like A Critique For Ecology, but with lots of positive bits to go along with the critical bits and without a single narrow prescription for how to do ecology properly”, you won’t be too far off. The target audience is ecologists and ecology grad students interested in fundamental research.
Introduction: Nobody can agree on what ecology is or how to do it. Good.
Ecology has long been plagued by two linked anxieties: that we don’t know what it is, and we don’t know how to do it.
It may seem preposterous to claim that ecologists worry about what ecology is. Open any ecology textbook, and right in front you’ll see ecology defined as “the study of living organisms and their interactions with one another and their environment”, or words to that effect. Except that, when you read the rest of the textbook to discover what that means, you’ll find a heterogeneous mix of material that puzzles many newcomers to the field (Vellend 2016). How do chapters on levels of hierarchical organization (individual organisms, populations, communities), abstract concepts like food webs, and processes as different as evolution, competition, and energy flow all fit together into a unified whole? The answer to that question might well be “They don’t.” Philosopher of science Gregory Cooper (2003) devoted an entire book to searching for an adequate definition of “ecology”—and settled on a definition that arguably excludes entire subfields!
That ecologists worry that they don’t know how to do ecology might seem equally preposterous. And it is a bit imprecise. Actually, every ecologist thinks he or she knows how to do ecology—and that it’s only other ecologists who don’t. At least, that’s the impression one gets from reading what ecologists have said about how to do ecology. Ecology in the 1960s either made a great leap forward under the influence of Robert MacArthur and his emphasis on discovering and explaining general patterns (Brown 1997), or it made a great leap forward in the 1980s and 90s once it quit focusing on static patterns and started worrying about dynamics (Kareiva 1997). Testing alternative hypotheses in ecology either is possible only rarely (Quinn and Dunham 1983), or often (Loehle 1987). Small-scale field experiments either reveal the mechanisms driving ecological phenomena (Paine 1977), or are of limited use because all the interesting and important phenomena happen on larger spatial scales on which replicated experiments are impossible and on which idiosyncratic local details average out (Brown and Maurer 1989). Ecology’s increasing emphasis on mathematical theory has either increased the field’s rigor and allowed ecologists to ask interesting new questions (Caswell 1988, Scheiner and Willig 2011, Evans et al. 2013, Marquet et al. 2014), or has set ecology back by unmooring it from its foundation in natural history (Simberloff 1981, Dayton and Sala 2001). Meta-analysis either adds immense value by providing an objective statistical summary of the primary literature (Koricheva et al. 2013), or incentivizes “data parasites” to engage in question-free data dredging (Lindenmayer and Likens 2011, 2013). Experiments in artificial and semi-artificial systems such as laboratory microcosms either allow ecologists to obtain unique and valuable data that couldn’t be obtained any other way (Gause 1934, Lawton 1996, Morin 1998, Fox 2011, Drake and Kramer 2012), or are too unrealistic and artifactual to teach us anything about how nature works (Carpenter 1996, Krebs 2015). And so on.
Both anxieties reflect ecology’s development from historically-disparate sources (Kingsland 1995). Ecologists are and always have been heterogeneous in their motivations and goals, and thus in their methods. To read the founders of modern ecology—Tansley, Cowles, Shelford, Forbes, Lotka, Volterra, Gause, Clements, Gleason, Elton, et al.—is to be struck by their differences in terms of the questions they asked and how they went about answering them. Indeed, in the absence of any other information you’d probably be surprised to learn that they all are among the founders of the same scientific field! Those profound differences in motivation, methods, and goals are still with us today. This is very much in contrast with, say, evolutionary biology. The founders of evolutionary biology—Darwin, Wallace, Hooker, Huxley, et al.—largely agreed on what questions to ask and how to go about answering them, even as they sometimes disagreed on which answers were correct. The same could be said of the architects of the Modern Synthesis in evolutionary biology: Fisher, Haldane, Wright, et al.
Proposals to address these two anxieties tend to run to type. One type argues that ecology is, or should be, about discovering universal laws analogous to the laws of physics, or else that ecology is about discovering general principles and empirical regularities that play much the same scientific role as physical laws. To fail to discover the generalities hidden beneath the apparent polyglot variety of living organisms and their environments would condemn ecology to be nothing but a series of unique, unrelated case studies—a mere stamp collection. Stamp collecting isn’t a science. Proposals of this type include MacArthur (1972), Brown (1997), Lawton (1999), Murray (2000), Turchin (2001), Berryman (2003), Colyvan and Ginzburg (2003), O’Hara (2005), Scheiner and Willig (2007), Dodds (2009), and Harte (2015).
A second type of proposal inverts the first, arguing that there are no universal laws or other important generalities to be discovered in ecology, and that attempts to find them are useless at best. Rather, ecology is a science of unique case studies, and that’s a good thing. Successful case studies allow ecologists to predict and control the behavior of specific ecological systems. This is essential if ecology is to comprise more than just empty word games and ungrounded speculation, and if ecology is to be useful for conservation and management. The generality in ecology concerns not ecology itself, but how how ecologists should do ecology. There are universally-applicable methods that ecologists can use to study any particular system. Peters (1991), Schrader-Frechette and McCoy (1993), Kareiva (1997), and Simberloff (2004) are proposals of this type.
My thesis is that both types of proposal are wrong—and right.
The mere fact that those two anxieties—about what ecology is and how to do it—exist at all make it hard to imagine that they could be resolved by either type of proposal. Proposals that ecology is about the search for generalities, and proposals that it’s about applying general methods to specific situations, share the assumptions that ecology is one thing, and that there is one right way to do it. But if there really was one Correct Definition of “ecology” and one Right Way to do it, we’d likely have agreed on it by now. After all, consider the alternative: that there is one Correct Definition of ecology and one Right Way to do it, but for some reason we can’t all agree on it even though we’ve been doing ecology for over a century (ecology as a discipline dates back at least as far as the founding of the British Ecological Society in 1913). I find that alternative both too implausible and too depressing to contemplate. It suggests either that ecology as a field is deeply and permanently dysfunctional despite being comprised of extremely smart and hardworking ecologists, or else that many of those smart, hardworking ecologists are nevertheless deeply and permanently mistaken about how to do ecology. I will instead argue for a far more plausible and happier possibility: that the existence of ongoing disagreement about what ecology is and how to do it suggests that both sides have a point. Both are right in some respects or in some circumstances, and wrong in other respects or circumstances.
Indeed, I would go one step further and argue that ongoing disagreement among ecologists about what ecology is and how to do it is not a sign of the weakness of ecology, but a sign of strength. In my view, the diversity of ecologists’ motivations, goals, expertise, and approaches gives the field a collective vigor it would otherwise lack. A diverse field of ecologists can solve more and a wider range of problems than any single type of ecologist could, and can solve problems that would be intractable to any single type of ecologist or even any collaborative group. Ecologists know that no single living organism can be well-adapted to all environments or perform all ecosystem functions and processes on which life depends, and that for this reason diverse groups of organisms often will function better than less-diverse groups. An analogous argument applies to ecologists themselves. There isn’t just one sort of ecology that’s worth doing—there are several (at least), each of which can best be pursued via a characteristic mixture of complementary approaches. Which is why it’s a good thing that ecology has always been done by ecologists as different as Gause and Clements. Otherwise, much ecology that’s worth doing would go undone.
Which isn’t to say that there is no room for improvement, even great improvement. Ecology is hard. Changes in technology and other factors will create both new opportunities and new challenges for ecological research. And smart and hardworking as ecologists are they aren’t infallible (me very much included!) There’s never any shame in asking, “How are we doing, and could we be doing better?” And no personal criticism of anyone is implied by asking that question.
That question lacks a single, simple answer. There is no infallible, step-by-step recipe for Doing Good Ecology. But nor is it a case of anything goes. There may not be hard and fast rules, but I will argue that there are context-dependent rules of thumb that can be identified via a comparative approach. Researchers on different ecological topics often use the same research approaches. Each research approach has its own characteristic strengths, limitations, and “failure modes” (ways in which it tends to go wrong, when it does go wrong). For instance, ecologists working on many different topics have attempted to infer process from pattern—to infer from observational data the processes that generated those data, and even what data would have been generated had different processes been at work. Any ecologist attempting to infer process from pattern can learn something from other attempts to do so. It is inefficient for ecologists working on different topics to independently reinvent the wheel—and independently rediscover the circumstances in which the wheel is likely to get stuck. Throughout the book, I use a comparative approach to illustrate the characteristic strengths, limitations, and failure modes of different research approaches. The goal is to help ecologists do more of what works and less of what doesn’t.
[Overview of book goes here; I left it out because it’s currently in flux; I’m revising the chapter outline from my original book proposal.]
One inspiration for the book is history and philosophy of science, particularly philosophy of science grounded in actual scientific practice rather than in some hypothetical ideal (e.g., the work of William Wimsatt and Lindley Darden). Philosophy of science is infamous for failing to discover clear-cut, non-obvious, universal rules of good scientific practice. But as philosophers of science have recognized over the past few decades, that just means that doing good science is a matter of making professional judgments as to what questions to ask and how to go about answering them. Such judgments are context-dependent and contestable, and so always leave scope for reasonable disagreement (as any scientist who has ever experienced the peer review system knows!) But nor are those judgments purely subjective or arbitrary, like a preference for tea over coffee. This book is not a philosophy book, but I hope that this book will help readers make better judgments, even though no reader’s judgments will fully agree with my own. It is tremendously important to both science and society that ecologists have good judgment about what questions to ask and how to answer them.
A second inspiration for the book is Nate Silver’s The Signal and the Noise. It is a popular comparative study of prediction. Silver considers attempts to predict everything from the weather to sporting contests to elections to earthquakes. He concludes that there is no single recipe for successful (or unsuccessful) prediction, because many factors are helpful in some contexts and hindrances in others. Both Silver’s general approach and his conclusions are a model for my proposed work. I too consider a wide range of cases within a circumscribed domain, from which I draw general but context-dependent lessons.
A third inspiration is my blog. Since 2011 I have been blogging about many of the topics covered in this book, first at Oikos Blog and since 2012 at Dynamic Ecology (dynamicecology.wordpress.com). When I began blogging, I had no plans to write a book. But having been blogging for several years, I have realized that there are themes to which I keep returning, and that link together many of my posts. My goal in writing this book has been to pull those themes together and weave them together along with new material into a unified body of work. Blogging also has been extremely helpful by providing a forum to “think out loud” and discuss ecology with a wide range of ecologists. The commenters at Dynamic Ecology comprise a larger and more diverse group than I ever could have interacted with via scientific conferences (valuable as those have been to me as well). I have learned a tremendous amount over the years from our commenters, and especially from my blogging colleagues Brian McGill and Meghan Duffy. Plus, I’ve written more than a book’s worth of words on my blog already (probably over 100,000), so writing a book no longer seems as daunting as it once would have.
Writing this sort of book arguably is some combination of hubristic and foolhardy. Why should I—never mind anyone else!—think that I know enough about ecology to offer unasked-for advice on how to do it? That’s a good question, the answer to which has several parts. First, I’m a reasonably successful and experienced ecologist. Any reasonably successful and experienced scientist will have a thoughtful point of view on how to pursue research in their field. So if I’m not much more qualified than the average ecologist to write this sort of book, well, I don’t think I’m any less qualified. Second, as noted above I don’t have any strongly-held view on what exactly ecology is, and I don’t think there’s one right way to do it. That makes me different from at least some of the ecologists who’ve participated most prominently in what I think has become a stale and overly-polarized debate about what ecology is and how to do it. One of my motivations for writing this book is that I don’t recognize myself, or a lot of ecological research I admire, in calls for ecologists to focus on general laws, or in opposing calls for system-specific case studies. I find both those views too extreme. I’m a passionate moderate, to borrow philosopher Susan Haack’s (1998) self-description. Third, as noted above my experience as a blogger gives me some confidence that I have something to say that others will want to read. Longtime readers of Dynamic Ecology will find some of the material in this book familiar. But much of it is new, and all of it is woven together in a way that I believe adds value. A book is a coherent whole in a way a blog can never be. Finally, I’m under no illusions that everyone or even anyone will agree with everything I write (that really would be hubristic and foolhardy). Rather, I hope that readers will find what I have to say to be thought-provoking.
[Thanks to everyone who helped me goes here.]