Are there holes in ecological “research space”?

When faced with a set of items that can vary along multiple axes or dimensions, it’s often interesting to locate the items in a multidimensional space. Not just to see where they fall, but to see where they don’t–where are the “holes” in multidimensional space? Ecologists do this with species composition data, looking for “forbidden combinations” of species that perhaps can’t coexist because of competition. They do it with morphological data, looking for unoccupied areas of “morphospace” that evolution has failed to fill, possibly because of character displacement, or because of constraints that make it hard to evolve certain combinations of morphological features. And we can do the same thing with our own research!

Steve Walker gave me this idea, in his fun old post classifying different philosophies of statistics in a four-dimensional space. I’ve been wanting to apply the same idea to ecological research projects for a while now, just for fun but also to provide a basis for thinking about serious issues like how the field of ecology has moved through “research space” over time. I’m going to stick to four dimensions, because that seems like enough to be interesting, but not so many as to be overwhelming. So here are four dimensions along which empirical ecological research projects can vary:

  • Is the research conducted by an individual or small group, or by a large, coordinated team?
  • Is this research question- or hypothesis-driven, or not?
  • Is the research based on observational data, or data from manipulative experiments?
  • Does the research involve collecting new data, or is it based on existing data?

I could’ve added a fifth dimension for whether the research is empirical, theoretical, or a mix. And perhaps a sixth dimension for whether the research involves expensive equipment or not (think, e.g., whole-genome sequencing or high-tech remote sensing, vs. the low-tech gear used in much standard field ecology). And I could’ve added dimensions for spatial and temporal grain and extent. But like I said, four axes seemed like enough as a starting point. Feel free to suggest other dimensions in the comments.

To keep things simple, I’m going to pretend that there are only two possible locations on each axis. I don’t think much would be gained (in terms of either fun, or actual insight) by trying to be more quantitative than that right now. So I’m proposing a four-dimensional space with a total of 2^4=16 possible locations.

Here’s where I think various sorts of ecological research fall in that space:

  • A typical single-investigator grant from an agency like NSF, NSERC, or NERC involves an individual investigator, doing hypothesis-driven research (hard to get funded without hypotheses!), and collecting new data, either experimental, observational, or both.
  • NutNet is a coordinated team, doing hypothesis-driven research and collecting both new experimental and observational data.
  • An NCEAS working group is a coordinated team, doing hypothesis-driven research (at least usually), based on existing observational or experimental data
  • NEON comprises coordinated teams, doing hypothesis-free research based on collecting new observational data. Other large monitoring efforts like the Breeding Bird Survey, the Christmas Bird Counts, and coordinated citizen science efforts to monitor things like flowering phenology also fall into this category. Further back, the IBP basically fell into this category.
  • LTER sites are a bit difficult to classify, because in some ways they can be thought of as single (complex) research projects, and in other ways they can be thought of as a bunch of separate research projects that all just happen to occur at the same location. I guess I’d classify them as coordinated teams, conducting both hypothesis-driven and hypothesis-free research (LTER sites host experiments, but also engage in monitoring), by collecting new observational and experimental data.
  • An individual who writes a review paper is an individual using existing data to pursue research that might be either hypothesis-driven or not, and based on either experimental or observational data. I do think all combinations are possible here, although hypothesis-free reviews are probably fairly rare these days, and hypothesis-free reviews of experimental data are a bit difficult to imagine.

If you’re scoring at home, the above examples (which are merely the first ones that occurred to me) collectively cover 12 of the 16 locations in our four-dimensional space. The four gaps are as follows:

  • Individuals doing hypothesis-free research based on collecting new observational data. This is basically the sort of work with which ecology began–think of amateur naturalists in Darwin’s day, just observing and collecting the local flora and fauna. I’m sure there probably are individuals still doing this sort of research. But because of the inherent limits to how much data a single individual or small group can collect, this sort of work doesn’t figure very prominently in modern ecology.
  • Individuals doing hypothesis-free research based on collecting new experimental data. Pretty rare for people to do totally hypothesis-free experiments, just “kicking the system to see who yells”, as my undergrad advisor once put it. And quite rightly–this usually isn’t a very good way to do science, although there are limited contexts in which it can be useful.
  • Coordinated teams doing hypothesis-free research based on existing observational or experimental data. Have there been working groups, at NCEAS or elsewhere, just doing purely descriptive work? Or maybe exploratory working groups could be put in this category?

Wasn’t sure what I’d find when I started to think about this. But I think it turned out kind of neat. While the 12 “occupied” points I identified aren’t all equally occupied (as I noted, hypothesis-free research by individuals, based on existing data, is probably rare), I do think that they’re mostly more occupied than the four “gaps” I identified. And it seems to me that the four gaps exist for good reasons. They’re the four research approaches of the most limited scientific value, I think. In general, it seems like the gaps, and the more lightly-occupied parts of the space, are the “hypothesis-free” parts.  I also think it’s interesting that my four dimensions appear to be largely orthogonal. It’s not that, say, large coordinated teams only fall in one or two locations on the other axes or anything like that. And while I’m sure the relative occupancy of different points in this space has varied over time, I don’t think there are any occupied points that until recently were complete gaps.

What do you make of this?

41 thoughts on “Are there holes in ecological “research space”?

  1. Another great “get-em-thinking” post Jeremy, thanks.

    Don’t have an answer/opinion right now but I do think that your third axis needs a third element in it’s domain: research based on model experiments. Lots of people doing that, and in opposition to much empirically-based research, it’s also something that can be done solo fairly readily in many cases. Or perhaps make the dichotomy “empirical vs theoretical research” if you want to keep the full domain to 2^4 possibilities.

  2. You might still see some of your first bullet point gap in microbial ecology. I would consider the second bullet point the realm of “natural experiments” (sensu Holling, Carpenter, etc). Basically humans are imposing these non-hypothesis-driven experiments all the time.

    • Well, I suppose that depends on if you consider “natural experiments” to be “experiments”. 😉 I tend to think of them as observational studies. This is another place where maybe it would pay to go to an axis with more than two values on it.

      And yes, good point re: microbial ecology studies often filling my first gap. Probably any field that makes significant use of gene sequencing or other techniques were one lab can process a bunch of samples and produce a bunch of data is going to have studies that fill that gap.

      • I don’t think all “natural experiments” are alike by any means and therefore don’t think it’s a good idea to lump them all together. To some, a natural experiment just means recording whatever states nature throws at you. To others it means specifically trying to sample in such a way that you mimic, as well as you can, a manipulative experiment. Big difference between the two.

  3. It seems like points 1 and 3 are addressed by some of the citizen science projects. Specifically, I’m thinking of the Christmas Bird Count, the Breeding Bird Survey and eBird – all involve gathering ‘pure’ observation data and each starts at an individual level (personal or small groups). The data is then organized into a larger project and made available for amateurs/professionals to play with. Similar projects involve recording amphibian calls and butterflies.

    • True, but as I said in the post, I think big citizen science projects like the BBS are best thought of as being conducted by coordinated teams. The central coordination is important–the individuals who collect the data are obliged to collect centrally-prescribed data in a centrally-prescribed manner.

      • I guess? I mean if you have no coordination than how can you do science?

        But okay, then I’ll just say that birders (before they enter their data into eBird) are doing personal observations without hypotheses-generation. There are probably many ‘field notebooks’ (not official ones obviously) filled with observations including dates, times, places of birds (“first robin of the season today!”; “weird to see a snowy owl down here”; “no birds singing today (weather = windy)”).

      • It sounds a bit like you’d like to see another axis here, something like “conducted by amateurs” vs. “conducted by professionals”?

  4. Individuals doing hypothesis-free research based on collecting new experimental data. Pretty rare for people to do totally hypothesis-free experiments, just “kicking the system to see who yells”, as my undergrad advisor once put it. And quite rightly–this usually isn’t a very good way to do science, although there are limited contexts in which it can be useful.

    Heh. That’s funny. In the next few weeks I’m building just the opposite argument 🙂

  5. I think you may not see much of the “Individuals and coordinated teams doing hypothesis-free research based on collecting new observational data” because much of that sort of thing falls outside traditional academia. I’m doing a fellowship in an entomology department at a museum right now, and this is exactly the sort of thing that many folks here do: go out and collect insects all over the world just to see what’s there and see if they discover anything new. You might not classify this as “ecology,” but you’d probably also classify as “natural history” and not “ecology” most things that fall in this category just by definition. While there is plenty of collecting going on, there’s also some actual ecology, as well. For example, there’s a big effort in Papua New Guinea to not only collect and identify all the different insects that exist there, but also to figure out what they all eat so as to determine the food web structure.

    And I’d like to add a physical location axis to your space — maybe just latitude would be fine. I think you’re more likely to see observational ecology in the tropics and other areas of the world that are ecologist-poor relative to North America and Europe.

    • Alpha taxonomy is thought to be valuable, but “alpha ecology” – aka natural history – not so much. One of these days, I dream, a review of a manuscript will not use “natural history” as an epithet.

      • Well, there’s Am Nat’s natural history notes section, which focuses mostly on natural history that’s somehow unusual or has some other “hook”. And Nature’s late lamented “brief communications” sometimes used to publish the same sorts of papers. An former undergrad prof of mine, a botanist, did one of those on a unique method of ballistic seed dispersal used by a plant she studies. The hook was that it set some kind of record for strongest ballistic force ever produced by a plant or something. And Journal of Ecology I think still devotes space every issue to a natural historical description of some plant species native to the British Isles. But it’s of course true that leading ecology journals don’t devote much space to natural history.

        I suppose one could say that the natural history in a lot of papers published in leading ecology journal is implicit. Lots of people publishing papers in journals like Ecology Letters and Ecology do in fact know lots of natural history, and say it’s part of the foundation of their work. But like the foundation of a house, it’s out of sight. And it’s not the focus, in the sense that it needs to be there (otherwise the house wouldn’t stand up), but it’s ultimately just there to support the house and isn’t considered to be of interest in its own right.

        Another way to put the same thought is to say is that natural history is related to but distinct from the sort of science that mostly gets published in leading ecology journals these days. So that leading ecology journals don’t publish much natural history for the same reasons that they don’t publish much material from other related but distinct areas of human activity.

        I’m just thinking off the top of my head here. And I agree that it’s a shame for people to devalue any activity different than the one they prefer to engage in, simply because it’s different. But at the same time, I do think there are arguably good reasons why leading ecology journals don’t publish much natural history. That is, there might well be good reasons to consider “natural history” and “ecology” as related but distinct activities. So that one might well want journals devoted to one, and different journals devoted to the other. Much as we have different journals devoted to, say, ecology and evolution, even though those fields obviously are very closely related and many people read journals in both fields.

        I agree with you that it’s a shame for anyone to use “natural history” as an epithet. But if someone reviewing a paper says that “this paper is excellent natural history, but it’s not excellent ecology”, that might not be an epithet, it might just be a correct description. Much as a paper I recently sent to Evolution got negative reviews in part because reviewers questioned whether it was really an evolution paper or actually an ecology paper. I disagreed with those comments–I thought it really was an evolution paper, which is why I sent it to Evolution–but I didn’t consider the comments unfair, or as devaluing ecology as a field.

      • I agree that academic ecology is (or at least, has become) distinct from natural history. Ecology outgrew natural history into something else. and now there isn’t a formal venue for natural history. But unlike phrenology, there remains a real value and importance of natural history.

        Ecology journals don’t want you to include any natural history observations unless they are absolutely critical to the point of the paper. For instance, in the context of a litter/ant project we were able to measure the densities of a very cryptic (and deadly) snake within our plots, over a wide geographic extent that hadn’t been measured by herpers. Both reviewers, and the editor, said that it was off topic and occupied otherwise valuable space in the journal. I’m not going to write that up as a little note in a herp journal, which means that this observation has disappeared to history, when otherwise it couldn’t have. I’ve mentioned it as an aside in talks, and people ask me where they can cite that – but they can’t.

        As a reviewer and an editor, I’m sensitive to this concern about relevance, but I also am pleased to let folks include natural history bites in papers.

      • So you’d probably be annoyed by one piece of advice from an old post of mine on how to give a good talk: omit natural history information unless it’s directly relevant, or at most just give a little bit of extraneous natural history detail. Because like all extraneous detail, it interrupts the flow of the story. And I’m sure any journal in any field would take the same view. It’s not that ecology journals are uniquely opposed to publishing asides.

        So sorry, I’m with your reviewers on this one: that observation about snake densities doesn’t belong in an ant paper, not because it’s extraneous natural history but just because it’s extraneous. If I were a reviewer and you threw in an extraneous aside that was about mathematical theory, or some other ant species, or whatever, I’d tell you to cut that too.

        And as for the observation now being lost to history, no it won’t be, not if you publish it. Indeed, it’s surely more likely to reach herpetologists if you publish in a small herp journal than if you publish it as an aside in a paper about ants, even an ant paper published in a leading ecology journal. Or at least, it won’t be appreciably more or less lost to history if you publish in a natural history journal than if you publish as an aside in an ecology journal. After all, most published science ends up “lost to history” in the sense that it will be read by at most a few hundred people, and cited little if at all. That’s true whether you publish in Ecology Letters or in a natural history journal.

      • Not annoyed, but pleased to agree to disagree. I agree that staying on point is central to giving a good talk or writing a good paper. I also think that, in the methods, a single parenthetical sentence can be illustrative and accent rather than take away. from the aim (For example: while doing the sampling, we encountered X hog nose vipers, representing a density of Y/m2). If part of the message of the talk is about the extraordinary density of ants in the rainforest, an aside about the density of snakes works well.

        I think there are no natural history journals anymore, or so very few, because nobody’s doing it. That’s a whole genre of editorials unto itself.

      • I think there are still natural history journals, from the regional journals in the US (Southeastern Naturalist; Northeastern Naturalist; American Midland Naturalist; Southwestern Naturalist; Northwestern Naturalist; The Prairie Naturalist) to Canadian Field Naturalist. They publish some ecology, but they also publish quite a bit of observational natural history. Things with titles like “First records of least terns nesting on non-gravel roofs”, etc.

        Those aren’t places with profiles or impact factors that are going to get you a faculty job, or get you tenure, but they exist. But if it’s about getting a novel observation in print somewhere so someone else can use it, they’re valuable outlets. Would a flagship or high profile natural history journal be useful? Or even feasible? It’s something I had been curious if the Natural History Network might take on, but they’ve dedicated their journal more to natural history in education.

      • “Those aren’t places with profiles or impact factors that are going to get you a faculty job, or get you tenure…”

        And right there is the entire problem. Those who favor “ecology” over “natural history”, rarely taking the time to illuminate us on just where the demarcation line between them is, will give the obligatory “what a shame that natural history has declined” (read: “been shoved aside”), but they aren’t going to do anything about it, that’s for sure.

        Definitely with Terry on this issue.

      • Jim, I’m going to push back a bit here.

        As for where the line of demarcation is, how about an operational definition: ecology is the sort of thing that is taught in ecology courses, written about in ecology textbooks, and gets published in ecology journals?

        As I noted in a previous comment, plenty of ecologists do in fact know a lot of natural history, and that knowledge is absolutely essential to their work as ecologists. That a foundation of a house is only a means to the end of building a house, rather than an end in its own right, doesn’t mean that people don’t value or don’t care about the foundations of their houses. Darwin famously made heavy use of natural history observations, by himself and others, in his work. It would be hard to argue that Darwin didn’t value natural history! But he valued it, or at least came to value it, as a means to the end of pursuing evolutionary biology. Indeed, by inventing evolutionary biology as a field of science related to but distinct from natural history, Darwin arguably did as much as anyone to cause natural history to decline.

        More broadly, every field of science is now both much more professionalized and much more hypothesis-driven and (in fields where experimentation is possible) experiment-driven than it used to be. If natural history is no longer seen as having as much value in its own right as was once the case, well, the same is true in chemistry, physics, and most other fields of inquiry. If you want to understand why natural history has declined, I really think you ought to cast your net much more broadly. Natural history’s decline is merely one consequence of much broader and longer-term trends in how people study the world.

        And if ecology grew out of an activity (natural history) that used to be seen as more valuable than it is today, well, I still don’t see why ecologists are under a special obligation to argue for the value of natural history, publish in and cite natural history journals, etc. Every current field of human intellectual activity developed from some previously-existing field, and many of those previously-existing fields either no longer exist, or exist in highly-modified form. I don’t really see why those currently pursuing activity A are under an obligation to help encourage the ongoing pursuit of activity B, out of which activity A grew.

        I’m perfectly happy if natural historians want to argue for the ongoing value of natural history as an end in itself, as opposed to only a means to the end of doing ecology, or evolution, or whatever. And if there are ecologists and evolutionary biologists who also want to make that argument (and there are), I’m perfectly happy for them to make it. Just as I’d be perfectly happy if my ecologist colleagues were to speak up against, say, declining support for the arts and humanities by governments and academia. But what I don’t understand is that idea that all ecologists and evolutionary biologists are under some sort of special obligation to argue for and support natural history as an end in itself, just because ecology and evolutionary biology grew out of natural history. Nor do I understand why ecologists somehow deserve specific blame for the decline of natural history, when the rise of ecology and the decline of natural history are just instances of much broader and longer-term intellectual trends.

      • I agree, Jim – I publish descriptive natural history, and I’d like it to be valued more (rather than treated as a liability on the CV). But by its nature it tends to be taxon or region or system specific, and isn’t ever going to be highly visible or cited. I don’t know what to propose to make natural history easier to evaluate (by funding agencies, by tenure review committees) on its own merits – “alt metrics” (?) for species descriptions, or for inventory work, or for publishing a life history paper, or for novel observations of biology in the field. These are things that aren’t ever going to be cited much, but still likely differ from one paper to the next by merit or value.

        There’s no forthcoming sea change where science institutions are going to cease needing to evaluate the worth of our work; if you want to elevate the status of some kinds of research that fall under the natural history umbrella, you need to have some metric to show that it’s been used or that it’s interesting. As I said in my post: would a “flagship” natural history journal be worthwhile? Would it even be possible? What would its screening or reviewing criteria be? Could it possibly aspire to a reasonably high impact factor? Or could it be evaluated on different measures (readership, etc.)?

      • Good comment Eric, which I think leads to a broader point. Rather than lamenting that natural history isn’t “valued”, I think it’s worth thinking in terms of specific issues and how to address them.

        For instance, consider the issue of “how can I publish natural history observations in a form that will allow them to be found and used by anyone who’s interested?” Eric’s comment discusses a ‘flagship’ natural history journal. For at least some kinds of natural history data (particularly observations of occurrence or abundance), I think some sort of online, publicly-accessible, GenBank-type database would make sense. Indeed, such a database already exists for birds (eBird). And I’m sure there are other possible solutions here. Talking about specific, concrete issues facilitates discussion of specific, concrete solutions. In contrast, “Natural history needs to be valued” doesn’t strike me as an issue that’s sufficiently well-defined to be even potentially soluble (Who should value it? Why? In what way should they express their value of it? Etc.)

        Of course, just because an issue is concrete and specific doesn’t mean there are any feasible solutions. For instance, “How can we get research universities to hire more tenure-track faculty who are natural historians, as distinct from ecologists and evolutionary biologists who know and use natural history?” strikes me as an insoluble issue.

      • Part of my concern with the decline of natural history is that basic descriptive observations on organisms often are the foundation (per Jeremy) for the kind of trait-first work that people like Brian McGill advocate (and I generally buy that world view). For taxonomic groups that are historically under-studied or poorly known, we can’t get to functional or trait-based ecology at present, but we don’t have any incentives for people to do the basic descriptive natural history that ultimately becomes a trait database that ultimately becomes Ecology or Ecology Letters or Science papers in the future. So how do we get there? Jeremy would likely answer not to worry about those taxonomic groups; work in a system where your question is tractable. I think that’s probably fine (and likely good advice, really) for basic ecology, but less satisfying for applied ecology, management, and conservation.

        I’m interested in solutions to encourage and support some natural history work continuing, being published, and finding its way into ecology and evolution. There are certainly studies where you can build your own foundation and leave it implicit, but there are studies (macroecology, biogeography) where you’re aggregating an explicit foundation out of decades to centuries of work by an entire field. To my mind, still getting some natural history done and making it visible (whether in a journal, or through an online database, etc.) is going to have to work within our existing institutions. Lamenting that “natural history isn’t valued any more” isn’t going to get anything done; we need pragmatic solutions. There is undoubtedly still a need to generate some descriptive, observational data on organisms in nature; so how do you fund it (crowdsourcing? undergraduate theses? citizen scientists?)? where do you publish it? and how do you do it in a way that is at least career neutral (doesn’t hurt you), and preferably career positive?

  6. There are lots of hypothesis-free experimental studies in my area. Laboratory evolution studies like Lenski’s E coli or Ken Weber’s fruit flies or Ted Garland’s wheel running rats. Take Garland’s. Split an initial pop of rats into 8 lines and give half the lines access to wheels. Then breed the rats that spend the most time on the wheel. Garland probably has 50-60 papers from this system, none following any specific hypothesis from the outset. There are many many great results such as the evolution of different strategies given the new environment. Ditto Lenski’s long term evolution of e. coli. Split them into lines and let them evolve. Look at al the great stuff that system has revealed both ecology and evolution. These to me seem like systems that were kicked and who screamed was very very interesting

    • Very good point Jeff! Can’t believe I of all people forgot about work like Lenski’s, which I know very well and hugely admire!

      This perhaps deserves further commentary–what it is about these sorts of hypothesis-free evolutionary experiments that makes them interesting? Presumably, part of it is that they turn out to be relevant to the evaluation of various hypotheses (e.g., hypotheses about genetic and phenotypic parallelism in Lenski’s work). But I don’t think that’s all of it. What do you think?

      • Maybe humans just aren’t very good at being creative thinkers so the hypothesis-driven experiments that we create are a small subset of the population of interesting hypotheses to test. The long-term lab selection experiments are like hypothesis factories – they generate data that generates hypotheses that can then be tested experimentally. Hypotheses that just weren’t really thought of. The advantage of these to similar types of field experiments is that the system is so much more manipulatable and controlled. So I cannot think of a field system (like say the Trinidad guppies) that has really generated lots of new hypotheses that weren’t thought of at the outset. I would kill for a system like Lenski’s where I would grab generation 2500, bring them back to life, and tests aspects of their physiology, genetics, ecology, behavior or whatever.

      • Very, very late of course, but just noting for the record my recent online exchanges with Rich Lenski, in which he pointed out that his long-term evolution experiment had hypotheses from the very beginning (although it’s also thrown up many surprising results that weren’t hypothesized about in advance).

    • @Jeff Walker:

      I’m setting some kind of record for a belated reply here. But just stumbled across this old thread while looking for something else, and so wanted to note for the record that Rich Lenski’s long-term evolution experiment was *not* hypothesis-free:

      Yes, it’s thrown up many unanticipated surprises, and so served as a source of new hypotheses. But it was originally conceived as a test of existing hypotheses.

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