The most, and least, influential calls for future research in ecology

Many papers in ecology (and other fields) end with calls for future research. Sometimes those calls are vague as to exactly what future research is needed. Other times they’re calls to pursue very specific research programs.

Speaking as someone who has concluded papers with calls for future research, I have mixed feelings about such calls. On the one hand, new grad students love it when papers identify knowledge gaps, because the dissertation proposal writes itself. On the other hand, I feel like many calls for future research are basically useless (some of mine very much included!) “There are still things we don’t know about X, so further research is needed” is always true, for any X, and so is a totally unhelpful thing to say. After all, nobody ever writes “We now know everything there is to know about X; no further research is needed”! Plus, calls for future research are so numerous that many (most?) of them are bound to be ignored. We’re not short on ideas for future research! So surely only a tiny fraction of calls for future research are likely to be heeded by any substantial number of readers.

Hence my question: what are the most influential calls for future research in the history of ecology? Are there any cases where somebody called for research on X, and then a bunch of other people went out and did that research?

Conversely, what are the least influential calls for future research in the history of ecology? The topics on which people have repeatedly called for future research, only to be repeatedly ignored (hence the repeated calls!) At the ASN meeting in Asilomar a few months ago, Christopher Moore pointed out that theoreticians have spent decades calling for more models of the population dynamics of mutualists. So that’s a candidate for “least successful call for future research in the history of ecology”.



25 thoughts on “The most, and least, influential calls for future research in ecology

  1. Well, it’s not ecology, and not exactly a call for future research perhaps, but the concluding sentence of Watson and Crick (1953) takes some kind of prize for influence:

    “It has not escaped our notice that the specific pairing we have postulated immediately suggests a possible copying mechanism for the genetic material.”

      • Well, in the understated British way of writing in 1953 or so, I interpret it as saying “don’t stop with the structure: let’s figure out how it works”. Of course, they already knew, at least the beginnings of it.

  2. What would good alternatives be? Perhaps always suggesting specific future directions which are promising, as opposed to others? Or qualifying specific gains of certain research extensions? One thing common in the theory literature (which I’m also guilty of doing) is saying someone should look at extending the model to include X interaction or physical effect, or trying to generalize beyond needing Y assumption. Rarely is substantial effort given to saying why such extensions might be valuable. I think authors avoid that as it opens up reviewer criticisms like, “If X was so important, why didn’t you account for it?”

  3. In 1990, the ESA wrote the Sustainable Biosphere Initiative, led by J Lubchenco, A Olsen, LB Brubaker and SR Carpenter. I think this roadmap was quite influential at the time, but since very wide-ranging, it is hard to discern the larger impact. I personally used it as a basis for my first NSERC Discovery Application, which was successful, and used it OFTEN as a background for proposals in the five yrs following.

  4. Ha! This is an awesome question. When I write these calls, I’m always rephrasing in my head to say “Well, if I were working in this field (which, you know, I am!), I would be most interested in studying X.” Whether or not I actually end up studying X, it feels important to me that my readers know what I think is the true creative spark the work yields. Sometimes it’s because I *want* to study X but don’t yet know how, so it’s something of an appeal for help/community, especially if X requires skills I don’t have but others do. So equivalently, when I read these calls, personalizing them a bit in my imagination helps me, and I like them!

    • “I’m always rephrasing in my head to say “Well, if I were working in this field (which, you know, I am!), I would be most interested in studying X.””

      Heh. An early draft of this post said something like “Whenever I read a call for future research on X, I mentally translate it as ‘I, the author, personally plan to do further research on X.'” 🙂 I deleted it because I thought it sounded too snarky. Too critical of authors (including me!) who conclude their papers with calls for future research. As if the author was saying “I want to work on X, for idiosyncratic and purely personal reasons. I think everybody else should share my personal idiosyncrasies and work on X too.” It hadn’t occurred to me that, as a reader, I could react in a positive way to an author saying “I think the most interesting thing to work on next is X”. As you say, it’s a window into how an expert sees their field, and where they think it’s going next.

      • Right! It would all be a lot clearer if, as Steve Heard advocates for, we could be a bit more informal/personal in how we write in scientific papers!

  5. I’m writing the discussion of a paper right now, and trying to say something about future research directions. I think that an important aspect is the relationship between what you show in the paper and what you want to suggest as future research. What I’m trying to write is not so much “there are still things we don’t know about X so future research is needed” but rather “there are things that we don’t know about X but now, thanks to the wonderful results of this paper, we have the ability/perspective/methods/etc to make future research possible”. As you say, there are always things we don’t know about X. But did your paper change the situation? Did it allow questions to be asked about X that weren’t possible before? If so, pointing out those questions as research directions becomes a valuable service to the reader.

  6. Frederic Clements’s (1907) call for integrating physiological research into ecological research:

    > Ecology has been largely the descriptive study of vegetation; physiology has concerned itself with function; but, when carefully analyzed, both are seen to rest upon the same foundation. In each, the development is incomplete: ecology has so far been merely superficial, physiology too highly specialized. The one is chaotic and unsystematized, the other too often a minute study of function under abnormal circumstances. The greatest need of the former is the introduction of method and system, of the latter, a broadening of scope and new objectives. The growing recognition of the identity of the two makes it desirable to anticipate their final merging, and to formulate a system that will combine the good in each, and at the same time eliminate superficial and extreme tendencies In this connection, it becomes necessary to point out to ecologist and physiologist alike that, while they have been working on the confines of the same great field, each must familiarize himself with the work and methods of the other …. The ecologist is sadly in need of the more intimate and exact methods of the physiologist: the latter must take his experiments into the field, and must recognize more fully that function is but the middleman between habitat and plant. It seems probable that the final name for the whole field will be physiology, although the term ecology has distinct advantages of brevity and of meaning. (*Research Methods in Ecology* 1907, 1–2)

  7. I don’t think its accurate to say that the call to model mutualisms hasn’t been answered. I can immediately off the top of my head think of half a dozen papers that do this including one I authored. The problems are that: a) mutualism didn’t lend itself quite as easily as competition to modelling so the resulting models are more complex (have to involve not just the 2-way interaction but limitation by some additional 3rd factor resource) and b) mutualism covers a wide variety of interaction types (services and physiological) and the more successful models are more specialized. So I think the call has been answered and the answers demonstrated that we’ll never have the extremely simplistic, highly general models we have for competition (and to a somewhat lesser degree) for predation favored by May, MacArthur, Fox, etc. So the call was answered, just not in the way originally envisioned.

    • I actually agree with the general thrust of your remarks here, and I suspect Christopher Moore would as well. Which probably just illustrates that what seems like an unanswered call to some people seems like an answered call to others.

  8. I can’t think of a specific paper off the top of my head, but I can think of some edited volumes, and there have to be papers too, that called for the study of the ecological impacts of climate change (and conversely of the ecological influences on carbon cycling). Those calls have been answered by thousands of papers. But nobody traces them back as a response to some individual call. It seems to me science is driven by larger exogenous forces more than one individuals exhortation. I would think it would take an extraordinary confluence of timing, an influential individual, and a paper that was unusually widely read all at the same time for us to look back and say that paper really got listened to and everybody really picked up the research challenge it asked us too. The example above of Clements and physiology seems like another example. Did physiology get integrated into ecology because of Clement’s call, are a wide variety of exogenous forces including the emergency of ecology as a field with obvious ties to physiology, the increasing availability of instrumentation to explore physiological questions, etc.

    • “Those calls have been answered by thousands of papers. But nobody traces them back as a response to some individual call. ”

      Yeah, I had the same thought. The calls for future research that get answered are mostly those that are issued by lots of different people at the same time. Because, for exogenous reasons, it’s obvious to lots of people what the “next big research direction” should be.

      Which does suggest that individual researchers hoping to nudge the field in their preferred direction with a call for future research are probably wasting their breath. A single individual call do to X isn’t likely to move the needle on its own.

  9. In addition to whether the topic was considered worthy, I think part of the issue is if the call is vaguely or clearly written, for example “Further research is needed in this area” versus leaving the reader with a specific testable hypothesis that can be easily followed up. The former appears to expect a whole discipline to head in a certain direction whereas the other might create an achievable objective that 2-3 researchers can follow up.

    • I’d say that influential calls for future research need to be specific and tractable, while still being of wide interest to many researchers. I wouldn’t say there’s *necessarily* a trade-off between the specificity or tractability of the call for future research, and the number of researchers interested in the call.

      • I agree. I am not suggesting there is necessarily a trade-off nor specifying the number of researchers, just presenting two extremes as an example. Ultimately it depends upon the topic under consideration. I see that calls for future research are often vague and overly broad and could be more meaningful and useful, in certain circumstances, if more specific.

  10. Probably confounded by time too, not sure how far back you’re thinking in terms of history…emerging topics may yet to see the uptake of calls for more research? Ecosystem services is still a newish research field, and ecologists have been calling for more research into how ecological interactions contribute to ES for years. But perhaps wIth the exception of pollination, we still know very little about the ecology of most services (& disservices)….every year hundreds more papers get published with vague correlations & quantitative claims but no measurement of actual interactions & processes relevant to the services.

  11. Maybe not a call for future research of the sort envisioned in the post (I’m too lazy to go check), but Gary Polis’ Am Nat paper on the food web structure of his desert study system certainly prompted a lot of further research. Polis showed that his food web had a very different structure than most food webs that had been reported in the literature to that point–much more omnivory, much more cannibalism, etc. He argued, convincingly, that the mismatch between his data and previous data was because most previous data wasn’t very good. The sampling effort underpinning most previously reported food webs was too low, there were too many sampling biases, etc. A number of investigators followed in Polis’ footsteps, and put a lot of effort into thoroughly documenting who eats whom in various other study systems.

Leave a Comment

Fill in your details below or click an icon to log in: Logo

You are commenting using your account. Log Out /  Change )

Facebook photo

You are commenting using your Facebook account. Log Out /  Change )

Connecting to %s

This site uses Akismet to reduce spam. Learn how your comment data is processed.