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.