Nobody writes papers complaining about the state of ecology any more (do they?)

Earlier this week, I was interested to read Liam Bright arguing that his own field (analytic philosophy) is a degenerating research program, and that ongoing attempts to salvage it by making it “relevant” or “practical” aren’t likely to succeed.

Even if you don’t think your own field is degenerating, I think it can be good mental exercise to consider the possibility. I’ve done so in the past in a somewhat tongue in cheek way, designing an imaginary graduate course on whether ecology is f*cked or awesome. That imaginary graduate course mostly wasn’t based on my own concerns or complaints about the state of ecology. It was based on other people’s concerns and complaints.

I bring this up because, reading Liam Bright’s piece, it struck me that I haven’t read any similar critique from an ecologist in almost a decade, with the exception of pieces critiquing ecologists’ statistical methods. I mean, click that last link–most of the readings I proposed in the imaginary graduate course are old! Heck, most of them were old back when I wrote the post in 2016, and now they’re even older. And the few that aren’t old are either (i) about statistics, (ii) are pretty narrowly focused (e.g., critiques of NEON), or (iii) aren’t really about ecologists’ research practices at all (e.g., concerns about climate change).

Now, maybe I’ve missed a bunch of stuff (please tell me if I have!) And maybe I’m just wrong–maybe such pieces have always been rare events and they aren’t any rarer nowadays. But if I’m right that such pieces are rarer these days, why is that?

Maybe it’s because the field of ecology has grown more sophisticated in its statistical methods, and more focused on global change and conservation? So worries about our statistical methods loom large in our minds. Whereas worrying that global change or conservation research wasn’t worth doing would risk crossing the line from “good mental exercise” to “trolling”.

What do you think? Am I just off base here? (Quite possible!) And if I’m not off base, what do you think has changed?

p.s. If something’s changed, I don’t know that it’s necessarily a bad thing, or a good thing. It’d depend on the reasons for the change.

29 thoughts on “Nobody writes papers complaining about the state of ecology any more (do they?)

  1. Here’s a speculative hypothesis. The massive growth of the scientific literature and proliferation of scientific journals, combined with ecology’s already finely divided intellectual landscape (one person studies satellite-derived global patterns in primary productivity, another studies social structure of insect populations), means that ecology feels less and less like one unified thing, or at least it’s increasingly difficult to wrap your head around the whole beast. If ecologists do 10,000 loosely related things in as many different ways, and you only know about some of them, it’s hard to criticize the discipline as a whole. For that matter it’s hard to say *anything* about the discipline as a whole, unless the purpose is a cheerleading-type publication with a political angle (e.g., ecology needs more funding). As best I can tell, “Foundations of ecology” is not the required reading for grad students that it once was.

    Or maybe in the past people were given the latitude to define “ecology” as their own corner of the field (with a bit of a buffer), and they were really criticizing something much narrower than the entire field (e.g., a particular style of asking certain questions that generated many recent publications). Perhaps there are more targeted, recent critiques out there. In the world of conservation biology, someone sent me this article recently, which is somewhat along the lines of what you mention.

    Click to access Devictor%20%26%20Meinard_2019%20%281%29.pdf


    “discourses on biodiversity have become a rhetorical veneer hiding academic strategies to optimize funding and an opiate sustaining the comfortable belief that biodiversity knowledge unquestionably contributes to the mitigation of biodiversity loss.”

    • I agree with Mark. I regularly stuble on critique papers about specific ecology sub-disciplines or concepts (e.g., integrity). I do not think people complain about the state of physics or history as a whole. However, your question is still valid: Are reserachers complaining more or less about the state of their field. I do feel that many of us have a hard time being particularly critique of our own field of research, as we spend so much time explaining to funders how great it is.

      • “I do feel that many of us have a hard time being particularly critique of our own field of research, as we spend so much time explaining to funders how great it is.”

        Hasn’t that long been true, though? Is it more true today than it was decades ago?

      • Hasn’t that long been true, though?
        Yes, most probably. Although it was probably easier to shift your research back then: “I don’t think this subfield is going anywhere useful, so I will do something else”. Ecology researchers, like others, are increasingly specialized nowadays.

        Is it more true today than it was decades ago?
        I would say yes, because of the point above.

      • Interesting question. We need someone who was active decades ago to weigh in! To me it feels like we’ve ramped up the “ecology will save the world” rhetoric over time, which might come with enhanced disincentives for internal critiques, via an expectation of stronger pushback. But it’s hard to separate one’s own changing perspective (senior scientist vs. grad student) from real changes in the field. I guess that’s why we like data! Either way there’s an interesting dynamic there. A discipline that can’t handle internal criticism doesn’t seem like a healthy one to me, but there are optics to consider.

      • “A discipline that can’t handle internal criticism doesn’t seem like a healthy one to me, but there are optics to consider.”

        Have the optics of psychology’s ongoing replication crisis been good or bad for the field? I’d say good, but perhaps the optics vary depending on who’s looking.

  2. Together with a colleague, some years ago we wrote an opinion note entitled ‘Is the science of ecology stagnant?’, which we were unable to publish. This was due to negative responses by the editors, I would say they were very reluctant to accept that the discipline might be stagnating. We cited a discussion between James Brown (the ecologist) and Peter Kareiva at NCEAS about this issue. From time to time I think about refloating the note to trigger some discussion, but I am not in the mood. I can send the draft if anyone is interested.

  3. Hi Jeremy. Perhaps as in most walks of life, we have become more tribal. It is fine to criticize others, but not our own.. It is not rewarded. Peter Abrams, in my view, criticized some approaches in a completely well founded ways. People reacted negatively. Even criticizing methods is met with negative feelings, in my view. Imagine, for example, if I criticized the introduction of meta-analysis before we fully understood its shortcomings and challenges.
    I would not be surprised if there has been a trend in our culture away from viewing constructive criticism as personal conflict rather than task conflict. There is interesting psychology on this (see Hidden Brain episode — The Easiest Person to Fool). If we perceive that if we criticize a way our field is doing something that we will lower our standing in the field because we will be judged personally as being a complainer, well, there is a good reason not to do it.

  4. Great topic, Jeremy! Also, many thought provoking responses from your followers. While I would not allege ecology is f*****, I would argue it is experiencing a crisis, or more…

    First, I would say that the term “ecology” has been affixed in a willynilly way to a variety of subdisciplines. While fields like ecological landscaping, restoration ecology, industrial ecology & social ecology have merit, I do not view them as core ecological sciences. I believe these and related disciplines should be splintered off into a completely different genre, perhaps grouped as “applied ecological disciplines,” but not as science per se. I feel true ecological science is watered down by these subdisciplines, and vice-versa.

    Next, from my experience as a reviewer of many ecological journals, I feel like overall, ecology is lacking in the quality control of publications. That is not to say many ecological journals are not without good quality control measures, but orders of magnitude more publish material that is either of little consequence, incomplete, incoherent or otherwise inane. This entire “publish or perish” mantra has caused myriad investigators to pump out one manuscript after another- when often one comprehensive and relevant publication would have sufficed a year or so down the line. Worse still is when a series of small, related publications culminated in nothing of merit.

    Lastly- my biggest peve of all concerns the recent trend of ecologists to weave the science of ecology into political, social, religious & lifestyle modalities. I am nauseated every time I encounter this hogwash. At the top of my list is the near constant drumbeat alleging a “war on science”. Last I checked, chemists were not crucified, biologists were not blugeoned, and ecologists were not eviscerated, at least intentionally. If policymakers opt to ignore climate science, for example, they haven’t declared any war on ecology. They’re simply ignorant and should be voted out of office. More broadly, the arguments that ecology provides us justifications for anything from abortion, to gay marriage, alfalfa sprouts, vasectomies and beyond is utter gibberish.

    Ecology is one of the physical sciences, and we need to impress this upon our future generations of ecologists.

    • Re the first two issues, I can’t judge as net good or bad but I do think some of this arises from incentives placed on all academics and isn’t really up to individuals. It *seems* many departments can no longer expect the position of retiring faculty to be re-filled, unless they sell it as a novel scientific direction to the college. I’ve no idea how much this is historical vs due to the new economic model of universities, but I’m often seeing ecology TT job ads that span a big range of qualifications / topics (one listed science outreach, conservation field work, and developing mathematical tools; another for climate change adaptation mentioned ecological, social, and climate science). To the extent that I wonder whether or not committees have time to evaluate the full range of applicants + criteria well, and whether they’re getting the applicants they really want as often as in the past.

      But I don’t know if this impression is a real issue or just the product of a solo postdoc in 9mo of quarantine 🙂
      (has anyone scoured ecoevo job ad archives?)

      • I think a historical study of faculty job ads in ecology would be interesting but probably infeasible. The links to most old ads are probably broken. Maybe some are archived on the Wayback Machine, but I doubt that enough are to give you a decent sample size.

  5. Concomitant with sheer growth and increased specialization, I also wonder whether a smaller proportion of ecology pubs today vs 20 years ago deal with fundamental topics? Ie a greater amount of applied and interdisciplinary work.
    (current job market sure feels that way, though of course I have little reference)

    • Feels that way to me too, but I don’t have any data either. It’s hard to compile data on this. The studies that have tried have used very coarse categorizations of papers (for understandable reasons), so may only be capable of picking up very big shifts in the literature. IIRC, the data say that there are definitely more climate-related papers than there used to be in ecology, but beyond that I don’t recall.

  6. Jeremy, I would have said that Mark Vellend’s book was an implicit critique of community ecology. And then proposed a solution. So, maybe more effective than simply provoking a debate.

    But your question raised another for me. Do you think that ecologists thought more about what good science is, back ‘in the day’? I have rarely, if ever, had a conversation with my colleagues at UNB Saint John that explicitly addressed that question. It seems to me that we can only have a discussion about whether ecology is in trouble, if we have pretty specific ideas about what ‘good science’ looks like. Are ecologists not thinking about it? Or are they reluctant to state their opinion about what good science is because it smacks of arrogance or hubris. It’s always struck me that scientists are reluctant to be very prescriptive about what makes ‘good science’, in a way that chefs, race car drivers and teachers are not.

    • “I would have said that Mark Vellend’s book was an implicit critique of community ecology. ”

      If Mark’s book was an implicit critique, then any paper that proposes a new conceptual framework is also an implicit critique. Anybody who says “here’s a new idea about X” is implicitly criticizing previous work for not having said everything worth saying about X. I think that’s an overbroad definition of “critique”.

      It’s fun (and difficult) to think in a comparative way about how willing people who do X are to evaluate what “good X” is.

      One hypothesis is that people are willing to talk prescriptively about what makes for good or bad X only in those cases where “good X” is easily recognized and widely agreed upon. Think of many sports, for instance. There’s not that much room for disagreement about what a good sprinter is (the faster, the better), or about who the best MLB player is (it’s Mike Trout). And people who care about sport X do in fact talk a lot about who the best athletes are and about what makes them the best. But on the other hand, there are plenty of other domains of life where people seem to talk a lot, and prescriptively, about what makes for “good X”. Even though “good X” isn’t measurable, or we can’t agree on how to measure it, or there are many different ways of being “good X” that can’t be boiled down to a unidimensional ranking. Think for instance of arguments about whether Hilary Clinton was a bad Presidential candidate who ran a bad campaign. Or think of all the arguments and anxiety about what makes for good parenting. Or arguments about which movies are good. So I dunno. I’m not sure what makes people willing to prescriptively evaluate some things and not others.

      • I guess I do think that any new conceptual framework is an implied criticism. Because the conceptual framework seems like it goes a long way towards defining what a discipline is. If community ecology requires a new conceptual framework that seems like a reasonably damning indictment to me.

        As for ballplayers – I think we would get a consensus on Mike Trout because we’re better at measuring what makes somebody a good ballplayer today than we were 40 or 50 years ago. In the 1970’s and 80’s Steve Garvey would have been routinely considered among the best players in the league (MVP once – top 10 in voting 5x), but that was before baseball really understood that batting average was not that important. Ecologists might get better at measuring what good science is if they started doing it. Or maybe we do…but we’re still at the point where we think “batting average” (number of pubs, amount of funding, number of citations) is important.

  7. Not that I’m aware of. Is there a scientific field that’s tried? Have we just accepted that it’s not possible? I’m puzzled that we’re willing to try and measure everything from the size of the universe, to the amount of a gene expressed, to human happiness…but ‘good science’ is inestimable?

    • Lots of things that we care about a lot aren’t measurable, even though we try. There are various measures that capture–very roughly–*some aspects* of “good ecology”. Citation counts, for instance. But I think evaluating “good ecology” is and always will be a matter of professional judgment. Not fully objective like measuring a mass on a balance, but also not totally subjective like a preference for blue shirts over red ones.

  8. The critique article by James Brown and commentary by Peter Kareiva are almost 25 yrs old. Since Jim spent the whole period doing the research program proposed in the article surely one can decide if The Metabolic Theory of Ecology lived up to its promise. And one can decide if Peter’s research program in applied ecology and movement ecology also worked out. Jim saw his as a specific component of Macroecology. In many ways the most important part of Jim’s critique is not the critique per se, but his suggestion as to the future directions. I dont know about the applied ecology of Kareiva, but Metabolic Ecology is doing just fine.

  9. Maybe related? One could explore similar issues at the lowest hierarchical level by inviting individual researchers to ask, “Is my research program f*cked?”

    I have been asking myself this question now that I’m in the last decade of my research career. The accounting includes some favorite and exciting discoveries, some papers and book chapters I loved writing, and a lot of successful trainees who went on to do great work in jobs and careers they love. In the other column are the research dead ends, the grant funds wasted on unproductive efforts, a few trainees whose careers did not thrive, and a lot of articles and book chapters that didn’t get cited much. On that negative side of the ledger is a decade-long effort to explore an important and interesting field of research that I extended into a new large taxonomic group: that effort didn’t generate enough interest to attract even one other researcher to ask the same questions in that same group of organisms. Basically, I threw a research party (and spent almost $100k on it), the drinks were cold and the music was dope, but nobody came.

    Maybe this kind of exit interview for senior researchers (before the exit from research altogether) could be helpful for ECRs to read and think about? And the public might deserve to hear from the horse’s mouth how things worked out with all that public research funding.

    • “the grant funds wasted on unproductive efforts”

      You could argue–correctly, I think–that if some grant funds aren’t wasted on dead ends, the funding agency isn’t taking enough risks. If everyone who gets a grant does exactly what they said they were going to do, and finds exactly what they said they expected to find, then it’s not research (as the old saying sort of goes).

      And if success depends on (or is defined as) attracting other researchers to follow your lead, well, don’t be too hard on yourself! Getting lots of other people who aren’t your own trainees to follow your lead is a big ask. Only a small minority of researchers are ever going to be able to pull that off, almost by definition.

      Your comments remind me a bit of Dennis Chitty’s memoir, Why Do Lemmings Commit Suicide? It’s an unusual scientific memoir, because it’s a story of self-admitted failure rather than a story of discovery. By his own admission, Chitty failed to answer the big question he spent his entire career trying to answer (why do small mammal populations often exhibit cycles in abundance?).

  10. My 2 cents: From what I see in marine ecology, much of ecological research can barely be said to have made much progress beyond technological improvements in the observations collected. As an example of what I’ve seen in my own career I’m working on four different projects right now:
    -one on shipworms – 400+ years of research, and still we have barely stabilised their systematics, much less tackled a reasonable explanation for their dynamics and distributions;
    -another project on molluscan shell growth will show how their growth has been mis-measured (and trends mis-interpreted) since the early 20th century because of over-reliance on von bertalanffy;
    -a third project is re-considering the concept of animal sentinels and their behaviors as marine environmental monitoring systems; much of this research has been driven by speculative statements in publications with scant evidence of cause-and-effect;
    -and a fourth has re-framed the socio-ecological system from a schematic drawing evoked in sociology and sustainability research, into a quantitative framework suitable for predicting long-term impacts of different economic activities.

    That said, it feels like ecology should be looking more to biology+evolution, physics and mathematics for inspiration these days, rather than re-hashing generic statements from the early days of biogeography and ecology. One reason for this is simple: (at least from my readings) it always seems that much of ecological research has “forgotten” that the mechanism of an ecological interaction happens between individuals. If we do not understand what the mechanism of the interaction(s) is/are, we will have great difficulty advancing toward a set of general laws/principles and a predictive, quantitative ecology. Ironically, some early marine ecologists recognised this, but biology was not able to deal with the questions they had about mechanisms at that time (1890s-1930s), so they backed off.

    Our frustration at encountering more rhetoric than evidence, has led us to launch a small initiative that aims to revise the fundamental practice of ecological studies to concentrate on individual-based approaches by re-starting new model frameworks from some of the ideas of Gleason, combined with recent advances in molecular and evolutionary biology and strongly grounded in physics. It’s leading us to make small changes (like not accepting students that refuse theory!) and moving experimental systems out of the laboratory into highly instrumented, densely observed real environments where we can embrace variability, instead of gumming it over with averaged values.

    On the other hand, we aren’t making a lot of friends, because our re-analyses keep showing how wrong some assumptions have been in the past. We think that students and researchers should be more aware of the fragility of many concepts and we would like to see more colleagues re-examine underlying assumptions in their work. It is surprising to see how few colleagues (and journal editors) are ready to talk about and re-consider fundamental ideas and issues. It is risky. The last time I wrote a proposal to do re-evaluate a theory the lab director actually wrote to the university president to cancel the project because another (senior) researcher was worried I might expose a flaw in his work. I couldn’t believe it when I saw the emails.

    So, anyway we are out here, and perhaps keeping a low profile for good reason …
    🙂

    • A lot of that sounds like the issue of “bandwagons” and which is also plaguing our internet-based world (politics etc) more broadly: simple and catchy black-and-white categorizations proliferate even though they cannot logically capture most of reality. Eg top-down vs bottom-up and whether invaders can provide ecosystem services.

      I think broad ecology journals these days value theory with tons of data over a pretty theory on its own? So larger and accessible datasets are part of the solution. But accommodating multiple hypotheses and mechanistic interactions in models (statistical and dynamical) is key as well. Teaching the latter means moving from quantitative courses that hammer in a few concepts (which work great on perfect experiments) into more independent, project-driven courses that build adaptability and collaboration.

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