Why don’t ecologists have more debates about alternative ways of studying X?

Here’s a recent blog post at Backreaction, pushing back against the arguments in high energy physics for a new, extremely expensive particle collider. I was most interested in the point that several of the purported scientific goals of a new collider could be achieved both more effectively and more cheaply with other sorts of equipment. For instance, if your goal is to look for proton decay, you can do that more effectively and cheaply by monitoring large tanks of water.

I’m not a particle physicist, so obviously I’m totally unqualified to evaluate these arguments. But I find them interesting to read anyway, because you don’t see these sorts of arguments very often in ecology. Indeed, they’re so rare that when they happen they become famous historical markers that get remembered for decades. Think for instance of the famous November 1983 issue of American Naturalist debating different approaches for studying interspecific competition. In ecology, it’s common for authors to argue for their own preferred approach to studying X. But I feel like it’s rare for authors to compare the pros and cons of different approaches. It’s commonly done for technical statistical debates such as data transformation vs. generalized linear models. And it’s sometimes done in review papers of non-statistical topics. But even there, it seems like reviews in ecology focus more on reconciling the results from different research approaches, less on evaluating the relative merits of different approaches.

Years ago, I complained about this in the context of using local-regional richness relationships to infer whether local species interactions limit local community membership. If that’s what you want to infer, well, in many systems you can just test that directly by experimentally adding species not currently present, perhaps also crossing the addition with some manipulation that reduces interspecific competition from resident species. See, e.g., Shurin (2000) for lake zooplankton, or the many, many terrestrial plant seed addition experiments and transplant experiments. Why use an indirect inference that depends on a lot of dubious and difficult-to-check background assumptions when you can just do a direct, straightforward experiment?* That’s just the first example that occurred to me off the top of my head. It seems like there are many contexts in ecology in which we ought to be debating the relative merits of alternative research approaches, but aren’t. Does anyone else feel that way? Or is it just me? (wouldn’t be the first time it’s just me…)

*And no, experiments aren’t always the best approach. My chosen example is just that–one example. The point of this post is not to argue that experiments are always and everywhere the Best Way to do ecology, because that’s not true and I don’t think that. I do think that, in general, scientists should prefer more direct approaches over less direct ones. As philosopher of science William Wimsatt points out, the more background assumptions and intermediate logical steps on which a conclusion depends, the less reliable it is, all else being equal.

7 thoughts on “Why don’t ecologists have more debates about alternative ways of studying X?

  1. There has been a lot of pushback on NEON, which is the probably closest thing ecologists have to a LHC-type project. Also considerable debate about simple vs complex models (Marquet et al. 2014 BioScience, Evans et al. 2013 TREE), or the utility of models in general. Or on the utility of mesocosms for understanding natural systems.

    • Yes, all good examples. But none of them feel quite like what I have in mind. Which just shows that I’m not really clear on exactly what I have in mind.

      I think part of it is that debates over simple vs. complex models, or microcosms/mesocosms vs. field studies, or NEON vs., um, stuff that’s not NEON, tend to be debates about the *general* merits of alternative approaches, rather than the merits of alternative ways of addressing a specific question. Put another way, they’re really debates about what our goals ought to be, not debates about how to achieve an agreed goal.

      Which is a little unfortunate, in that debates about how to achieve an agreed goal seem more likely to be resolvable, at least in principle. Once you strip away the post-hoc rationalizations, mutual misunderstandings, and bad arguments, debates about microcosms. vs. field studies, or NEON vs. not NEON, or whatever, are always going to come down to one side going “I just like approach X and the goals it can be used to achieve” and the other side going “I just like approach Y and the goals it can be used to achieve.”

      But then again, maybe the fact that a debate is resolvable in principle doesn’t make much difference to how resolvable it is in practice. From what I can tell, Sabine Hossenfelder is taking an enormous amount of crap from particle physicists for saying “if the goals of the next particle collider are X, Y, and Z, those goals can be achieved better and more cheaply in other ways.” Accusations that she’s not a team player, that she’s just a naysayer or defeatist, that she’s just trolling for attention…

      • Hi Jeremy; to quote you:
        ” Put another way, they’re really debates about what our goals ought to be, not debates about how to achieve an agreed goal”.

        I agree 100%, having been part to several such debates.

        BUT Please give us a few examples of ‘ agreed goals’;
        I doubt ecology has any, at least in the scientific sense.

        Particle physics has many, and the search for the time scale for proton decay has been a central question for decades [ yup, monitoring a big vat of water, etc].

  2. I appreciate this post, Jeremy — I often find these kinds of debates interesting and useful. An essay that I would enjoy reading, but may perhaps be hopelessly vague in concept, is an enumeration of all the broad classes of methods through which a trait can be found to be adaptive in a given environment, as well as their characteristic strengths and failure modes (if we can generalize that much). For example: experimental manipulation (of either the trait or the environment), observations over spatial or temporal variation, phylogenetic comparative methods, popgen-based methods, and mechanistic modeling based on underlying physics / chemistry. One could then discuss how these methods can help reinforce each other, and (perhaps most importantly) what to do when they yield incongruous results.

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