What unsolved problems will (or should) ecologists focus on in future, and how would you identify them today?

Writing in TREE, Mark Westoby reviews the new edited volume from Andy Dobson, Bob Holt, and David Tilman, Unsolved Problems In Ecology. He suggests that the volume is too backwards-looking:

Most of the authors write about their own current research topic. They have each had at least 10 years of research life, some of them 50 years, to think about ecology, to decide what are the most important questions, and to get organized to work on them. So a collection of contributors’ own research topics does, perhaps, reflect considered judgment about the most important questions for the future of ecology. Still, I would respectfully disagree with them. For me, most of this collection had the flavor of 1980–2020, not of 2020–2060.

Which raises two interesting questions.

First, when should a scientific field leave some problems unsolved? We’ve talked about this a bit in the past, in the context of ecological controversies. Sometimes, controversies get “resolved” because nobody has anything new to say about them, everyone stops caring, and the debate just fizzles out (perhaps until it gets revived in a different form a couple of decades later…). Are there some unsolved problems in ecology that are like that? Problems that we all ought to stop working on (at least for a while) because they’re intractable? Or, are there some unsolved problems we ought to stop working on because there are other, more urgent problems to solve? The field of ecology as a whole is increasingly voting with its feet, focusing on global change and other urgent applied problems (see here and here). But that trend has been going on for well over 20 years now. So if you want a book on unsolved problems in ecology that’s forward looking in the sense of “focuses on different problems than ecologists have been focusing on since the ’90s”, I don’t think it would be a book about topics like species range shifts under climate change, carbon sources and sinks, drivers of extinction risk, changing wildfire regimes, reserve design, etc. Though I suppose a book on those topics might still be forward looking in the sense of “correctly predicting the topics that ecologists will be focusing on in 2020-2060”. Because after all, maybe ecologists in 2020-2060 will mostly be focusing on the same global change-y topics they’ve been focusing on since the ’90s.

Second, how would you come up with a forward-looking edited volume? One that identifies the interesting and important questions ecologists will ask, or ought to ask, in 2020-2060? I mean, surely even very junior researchers are going to be most comfortable writing about their own research! And surely even very junior researchers think that their own research programs have bright futures and ought to be pursued by others (here’s some polling evidence for that)! I mean, I can’t recall ever reading a paper or book chapter in which someone says “Here’s an exciting new direction for ecology in future, which has nothing to do with what I personally work on”! So I think I respectfully disagree with Mark Westoby here. If the Dobson et al. volume does indeed have “the flavor of 1980-2020” (and as an aside, I can’t vouch that it does; I haven’t read it yet), well, I doubt that’s because the authors are mid-career and senior researchers who wrote about their own research. If you want a forward-looking edited volume on unsolved problems in ecology, that’s not about problems that many ecologists have been working on for years, you somehow need to identify researchers (junior or otherwise) who are working on problems that almost nobody else is currently working on, but that many people will (or should) start working on in future. Which seems both very cool and very difficult. For instance, look at awards for promising junior scientists, scholars, or artists–awards that aim to identify and boost creative people who will go on to do novel and outstanding work. Those awards mostly go to people who already have achieved some measure of mainstream success and recognition. So if you really want to identify the Next Big Thing in ecology, it seems like you’d need to take a venture capital approach. Take a lot of risks on the assumption that most of them won’t pan out. You’d want to produce an edited volume of really off the wall ideas, on the assumption that most of them will never amount to anything but that one or two will hit the big time. There is some precedent for such a volume.

10 thoughts on “What unsolved problems will (or should) ecologists focus on in future, and how would you identify them today?

  1. This seems like an appropriate context in which to resurrect Kuhnian paradigm shifts. Is it really possible for ecologists embedded in the current matrix of concepts, ideas, and theories to move outside that framework in a way that allows them to “see the future”? Kuhn would say no, and that we must rely on thinkers from outside the central core of our discipline to provide us with the necessary insight. In that vein, I am a bit skeptical that any responses received from the regular readers of Dynamic Ecology will move us very far beyond the bounds of our own research agendas. I would dearly love to be surprised….

    • This problem is why it is fun and often rewarding to venture into quite different areas, where you do not have the whole baggage of ‘known truths’ about methods and interpretations. Or for that matter, to read something completely out or your own fields.

      • I agree wholeheartedly. I would argue that it is not only fun and rewarding, but an intellectual prerequisite to avoid context dependency in our thinking. It is self-affirming to gain the depth of knowledge necessary to feel comfortable in a particular area of investigation, but the deepest revelations come when that framework is challenged by alternative views. In pedagogy, we strive to create moments of dissonance in student thinking where they are faced with ideas at odds with what they thought they knew about the world, but we often fail to take the same approach in our own work.

  2. We held a workshop here at Emory where we asked half the speakers to talk about an exciting direction in theoretical biophysics that they were not working on. I thought it worked pretty well!

  3. Interesting set of questions. I have not yet bought or read the book (although it looks like one I will buy), but I did skim it online (e.g. table of contents, some excerpts). It seems to me the chapter titles ask timeless questions (what controls the abundance of a population or the relative abundance of species in a community or how will organisms respond to climate change or how do we scale or what controls growth/productivity).

    I personally don’t have any problem with the notion that these large questions are pretty timeless and that ecologists will be working on them 100 years from now. I think at that level of coarseness one should expect continuity with just mild turnover in the set of big questions (e.g. not sure response to changing climate would have made the list 30 years ago but it is near the top of the list now).

    I think what Mark highlights is that once you get into the details of a chapter, most chapters pretty strongly show they are written by an expert in that particular field who has worked there for a long time. This makes it very hard (impossible?) not to have a healthy flavor of looking back as much as looking forward.

    I wonder what the book would have been like if each of the invited authors wrote a chapter title, and then they were shuffled so that each author was given another random title and asked to provide a forward looking overview of where we should head. I imagine that could have been rather novel and exciting (for sure the author list is among the brightest and most creative in the field), but of course not sure how many people would have volunteered to have to spend time doing a deep dig outside of their own subfield.

    • The “shuffle” approach sounds intriguing. As you suggest the time needed to dig deep enough to provide insights would be challenging so a significant time period would be needed between topic “assignment” and first draft. Perhaps one way to begin the process would be a symposium at ESA employing this strategy. Creating a mechanism for a dialogue between the “proposer” and the “commenter” once the talks were given might be interesting.

  4. The shuffled symposium sounds promising! But if you were participating, the chances would be fairly low that you’d get a topic where you felt you had something original to say. Maybe some sort of auction could be set up, where you got to bid for the topics that attracted you most? (Except not for the one you’d proposed yourself.)

    What would you bid with? — maybe you could promise reviews for whatever journal or society was organising the shuffled symposium. Three promised reviews beats two promised reviews, etc. And people who won’t promise reviews get stuck with the topics no-one else wants.

  5. Another potential source of ideas about the future of ecology (besides people’s own chosen research) is that most of us in universities get to decide what to teach within an undergrad ecology course. Fitted within (maybe) 26 lectures and a dozen pracs. So you get to think afresh each year about what’s important in ecology, what’s best and worst understood, and what’s maybe important but missing.

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