Posted by: Jeremy Fox | September 27, 2011

Why I don’t care what the biggest question in ecology is

Another tidbit from my interview with Sarcozona that got left on the cutting room floor. She asked me what I think is the biggest or most important question in ecology (something like that, anyway). I said that I don’t think that way. I think there are lots of interesting and important questions, and I have no idea how to rank them. But I don’t think the questions we choose are as important as how we go about answering them.

Back in 2000, there was a symposium at the ESA Annual Meeting on “30 Questions for Ecology in the New Century” (or something like that). The speakers were all very famous, but I don’t remember who they were or what they said. What I remember is the first talk I went to see after the symposium ended. It was by Peter Abrams, and he started his talk by saying “I predict that the 30 questions that occupy ecologists for the next 100 years will be the same 30 questions that occupied them for the last hundred years.” He got a big laugh, because he was probably right. And that doesn’t worry me at all (so when I laughed, it wasn’t because the alternative was to cry).

I don’t think the progress of our science is best measured by the questions we answer. Ecology isn’t a checklist (“Explain species-area curves–check! Explain latitudinal species richness gradient–check! Predict ecosystem responses to climate change–check!…”). Even if it were, the questions on the list would either change over time (nobody cared about climate change 50 years ago), or else would be the sorts of big, broad questions that by their nature will never be fully answered (“Explain distribution and abundance of species…hmm, let us get back to you on that…”) The progress of ecology is much better measured by improvements in our ability to answer whatever questions we want or need to answer. Indeed, I worry that, if we focus too much on trying to answer any one question, that narrowness of thought and focus will degrade our ability to answer other questions. As Peter Kareiva wrote in one of my favorite essays:

“Our future advances will not be concerned with universal laws, but instead with universal approaches to tackling particular problems, and with general theoretical insights about the surprises that may ambush us if we think too narrowly.”

Science isn’t a body of facts, it’s a body of methods. The most important thing we’ve learned is how to learn. What really matters isn’t our questions, it’s how we answer them.

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Responses

  1. I agree that the development of good methods is important. But some questions *are* much more important than others, because they have greater real world relevance. From a purely academic (ivory tower?) perspective, then yes, one question’s as important as any another (I suppose). From a real world problem solving perspective however, it’s not the case.

    I maintain that one of the biggest problems with academic science is how poorly (terribly!) integrated it is wrt real world problem solving. It often appears to me that there’s no strategy at all. It’s like every man (or research group) for himself, and the money chasing game is geared toward uniqueness/novelty of discovery, not societal relevance. I think figuring out what the most important questions are *and* also consciously developing the best methods to address them, is what we need.

    • Hi Jim,

      your response touches on some large and important issues, in particular “fundamental” vs. “applied” research, on which I’m planning to post at some point once I get my thoughts in order. A few brief comments:

      -I did not mean to argue solely for methodological development; what I (and Peter Kareiva) have in mind is much broader than that (my post was not especially clear on this)

      -fundamental research often is relevant to the solution of many different problems, but in diffuse and indirect ways.

      -What’s “relevant” changes over time, often quite fast. For that reason, specialists who have who only been trained to deal with and think about questions of current applied relevance often are poorly-prepared to deal with newly-relevant questions, and it is often impractical at best to rapidly shift training and hiring procedures in an attempt to tightly “track” changing policy priorities.

      -One function of fundamental research is to discover and evaluate the relevance of previously-unrecognized questions we didn’t even know we needed to ask. Researchers exclusively focused on addressing questions posed to them by policymakers are not necessarily best placed to recognize, or argue, that we are asking the wrong questions.

      -Related to the previous point, research directed towards solving particular applied problems tends to focus on a narrow range of solutions to those problems, and a narrow range of obstacles that might prevent those proposed solutions from working. Highly “relevant” research often is quite narrowly focused and fails to recognize useful linkages, analogies, and ideas drawn from other fields.

      I do not claim that we should not fund applied research, and deciding the appropriate mix of what to fund is probably impossible to decide based solely on the sorts of general considerations I have raised.

  2. Nice response Jeremy, and I generally agree with it. Much ink could be (and has been) spilled on the topic. Fundamental research definitely has its place, no question about it. I guess I feel that such could be more strategically planned/organized than it is, but this point is general and hard to demonstrate, and so it amounts simply to my opinion. We could probably use a blog devoted to this one topic alone!

  3. […] systems are so complicated, there’s an infinity of questions one could ask. And while I don’t think choice of question is the only thing that determines whether one’s researc…, I definitely believe that some questions are better than others. If you want to avoid jumping on […]


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