What are the biggest understudied topics in ecology?

Like politics, science is the art of the possible. Ideally, we’d collectively focus a lot of research effort on the biggest, most important, most interesting topics.* But some topics are more difficult to address than others, for all sorts of reasons.** Hence my question: what are the biggest understudied topics in ecology? The topics that are studied the least, relative to how big, interesting, and important they are?

Here’s my answer: non-stationarity. As far as I know, Peter Chesson is the only ecologist working on this. Which, if you’re just going to have one person working on this, is probably the right person! But really, I think it would be better if he had some help. 🙂

Warning: extended digression on non-stationarity coming up. Just skip to the end if you don’t care, and in the comments suggest your own big understudied topic.

To understand what non-stationarity is and why it’s important, you first have to understand stationarity. Stationarity has various technical definitions, but the gist is that a stationary system has some typical distribution of behavior in the long run. The mean, variance, and other statistical moments don’t change. A stationary system necessarily has some sort of return tendency–some process, analogous to negative density dependence, that keeps it from moving away from that stationary distribution of states.

Note that stationarity is a much broader concept than stable equilibrium. For instance, a population of jackalopes can be stationary even if it never reaches equilibrium (or even if it fluctuates irregularly or chaotically rather than in some regular cyclic fashion.) I’m totally unbothered that the world is non-equilibrial, because that doesn’t present any particularly difficult conceptual or practical obstacles. Plus, it raises various fun possibilities that wouldn’t exist in an equilibrial world. But non-stationarity–that worries me.

Stationarity matters because there’s a very large and well-developed toolbox of theoretical and empirical methods for studying the dynamics of stationary systems. For instance, Ziebarth et al. 2010 (a paper I love, so I keep linking to it) estimated the strength of population regulation for many different populations. That is, they assumed the populations were stationary, and used time series analysis techniques to estimate rates of return to stationarity. In general, it’s much easier to study something, theoretically and empirically, if it has some typical distribution of states or behavior. Roughly speaking, stationary systems are those that can be said to have typical behavior. A non-stationary system is one that doesn’t have any typical behavior.

Note that worrying about non-stationarity is not the same thing as worrying that short-term dynamics might be atypical or might differ from long-term dynamics. Every field ecology grad student’s worry that their first field season will be a “weird” year weather-wise is not a worry about non-stationarity. Worrying that this year your study system will be in a state that’s out in one tail of its stationary distribution (i.e. a state it’s rarely in) is not the same as worrying that your system has no stationary distribution. Nor is worrying that you’re observing transient dynamics rather than long-term dynamics the same thing as worrying about non-stationarity. Stationary systems can have transient dynamics that aren’t representative of the long-term stationary distribution. Nor is worrying that your system might exhibit different behaviors on different timescales the same thing as worrying about non-stationarity. Stationary systems can fluctuate differently on different timescales (e.g., daily vs. seasonal vs. year-to-year).***

I worry about non-stationarity because in a non-stationary world because many of our usual methods don’t apply. For starters, as far as I know most of our theoretical models, and the mathematical concepts and techniques used to analyze the long-term behavior of those models, go out the window. It’s not just that they don’t apply exactly, it’s that they don’t apply even approximately, or at all. Indeed, in a non-stationary world, many of the questions we ordinarily ask as ecologists don’t even make sense. For instance, what sense does it make to ask about coexistence in a non-stationary world? You can’t ask why species coexist if they’re not coexisting, merely co-occurring for some period of time. You can’t ask what their long-term average rates of increase when rare are if they have no long-term average rates. Or actually, you can ask some of those questions, but there’s no point to doing so, because the answers are going to change. You can perfectly well calculate the mean, variance, and other statistical moments of some finite realization of a non-stationary time series. But those numbers won’t tell you anything about what the series was like in the past or what it will be like in the future. In a non-stationary world, every period of time is unique, and so history becomes just one damned thing after another. You can do science about a unique series of one-off events, but it’s a totally different sort of science from the sort that many ecologists do. Conversely, in a non-stationary world other questions that we don’t often ask take on greater interest and importance. Brian suggests asking why non-stationary systems often seem to persist for such long periods of time, despite their non-stationarity. For instance, if species have non-stationary dynamics, how is it that the average species manages to persist for millions of years?

But don’t despair. There are various research strategies for a non-stationary world. Unfortunately, most of them involve working around non-stationarity than actually studying it.

  • Describe non-stationarity. Long-term monitoring is obviously an essential component of any research program on non-stationarity. But on its own it’s not very satisfying.
  • Focus on short-term dynamics. Think for instance of population viability analysis, key goals of which are to estimate the current rate of increase or decrease of some population we want to conserve, and predict the near-term effects of management interventions on population growth rate. This is much easier than trying to make long-term predictions about the population’s stationary dynamics, because you can safely assume that many things affecting the population growth rate (such as population structure) won’t change in the short term, at least not too much. (Aside: if you’re going to go this route, for the love of your deity of choice do it right. There are many weak studies of short-term dynamics in ecology.)
  • Study variables that have stationary dynamics. Think island biogeography theory: individual species come and go and might well have non-stationary dynamics, but species richness is stationary.
  • Find a spatial scale on which the dynamics are approximately stationary. For instance, in some metacommunity models you might well have non-stationary dynamics of individual species, and constant turnover of species composition within patches. But thanks to movement among patches, species richness, composition, and species abundances might be stationary at the larger spatial scale of the entire metacommunity.
  • Find a time scale on which the dynamics are approximately stationary. Stationary processes can look non-stationary if you don’t watch them for long enough. For instance, the famous 10-year cycle of Canadian lynx and snowshoe hares is stationary. But if you only had 5 years worth of lynx abundance data starting from the cycle nadir, it would look like a non-stationary increasing trend. Conversely, consider a system that is non-stationary only because it’s being exogenously forced by some non-stationary variable that changes very slowly relative to the other processes that affect the value of whatever variable you’re studying. You can consider that system to be stationary on time scales substantially faster than those of the exogenous driving variable.
  • Study variables and questions for which stationarity doesn’t matter. For instance, species abundance distributions have roughly the same predicted shape (lognormal or lognormal-ish) whether the underlying dynamics are dominated by drift or not. Pure drift is non-stationary. More broadly, there are many topics in ecology that have nothing to do with whether the world is non-stationary.
  • Treat a long-term trend as what’s “typical”. If the non-stationarity takes the form of a long-term trend in the mean, one can treat this trend line as what’s “typical”, and so ask questions about how long it will take the system to return to the long-term trend line following a perturbation, etc. That’s what macroeconomists do. For instance, US real per-capita GDP has grown at a long-term annual rate of 1.87% since at least the 1870s (figure), and so macroeconomists focus on perturbations away from, and recoveries to, that long-term trend line. I rarely see this done in ecology. Perhaps because there aren’t many ecological variables for which non-stationarity takes the form of long-term growth or decline?

Ok, that was a very long digression about non-stationarity. To wrap up, I want to return to the question I asked at the beginning: what are the biggest understudied topics in ecology? There was a time when “the microbiome” might’ve been a good answer, but not anymore. Same for “positive species interactions”. So, what’s your answer? Looking forward to your comments.

*Or, you know, not.

**Although the difficulty of addressing a question is not a fixed constant. Technological advances, creative insights, model systems, big grants, etc. can all make easy tractable what otherwise would’ve been intractable.

***One big practical challenge for studying a non-stationary world is figuring out whether you’re in one or not. Technically, stationarity is a property of the process that generated your data. Your data are merely a (finite) realization of that process, and it can be difficult or impossible to estimate the properties of that process from your finite data. Simple illustration: if you flip a coin four times and it comes up heads every time, you can’t infer from that whether the coin is fair or not; it’s not enough data to go on. Disagreement about whether we’re in a non-stationary world crops up often in ecology and evolution. For instance, it’s the crux of the debate about whether there are ecological limits to continental-scale species richness. I leave it to you to argue about what, if anything, the practical difficulty of distinguishing stationary from non-stationary processes implies for whether or how much we should worry about non-stationarity. I could see arguing this in at least three ways…

25 thoughts on “What are the biggest understudied topics in ecology?

  1. When we teach community ecology concepts in our general ecology classes, our theory is still rooted species equivalence, whether we are discussing species richness, turnover, successional processes, and so forth. And while we are collectively making progress with adding a phylogenetic framework to community ecology, we are not there yet. Not even close. While this is not the biggest understudied topic, is is the one most ripe for transformation in the coming decade.

    • “While this is not the biggest understudied topic”

      Yeah, hard to argue that phylogenetic community ecology is understudied at this point!

      “When we teach community ecology concepts in our general ecology classes, our theory is still rooted species equivalence”

      Not sure what you mean. Any ecology student learns that species vary in all sorts of ways. That some are much more abundant than others, for instance. That they have different diets (so food webs exist). Etc. The mere fact that we often consider species richness to be a variable of interest doesn’t indicate any big conceptual flaw in the discipline, I don’t think. At least not one the phylogenetic approaches are uniquely positioned to fix. Evolutionary history is just one way among others that species differ from one another. It might be important or useful to consider for some questions, but irrelevant or counterproductive for others.

  2. WRT to ” As far as I know, Peter Chesson is the only ecologist working on this.” I have to beg to differ. He may be the only person doing it from a predominantly theoretical point of view. But us more data-driven types have been talking about this for a decade or more. Really once, you get interested in time-series and you reject a stochastic equilibrium or a random walk, you have to talk about non-stationarity. EG I think Morgan Ernest is (and has been) talking about this whether she uses the word or not. I’ve got a book chapter showing pretty clearly that birds in the BBS are nonstationary (and I used the word pretty centrally). And that chapter is in a whole edited book on non-equilbrium dynamics in ecology (I know not identical but pretty closely related to non-stationarity). And I have a series of papers with Volker Bahn where we talk about non-stationarity in space as well as in time. And I have a paper with half a dozen coauthors that has languished in revision for years that is on phylogenetic nonstationarity. And in my database of papers I’ve read I’ve got a dozen or so I’ve tagged with the keyword nonstationarity. And writ very broadly anybody talking about global change is talking about nonstationarity.

    All of which is perhaps a long-winded, confrontational way to say that I agree with you this should be a central theme in ecology for a decade or two to come! 🙂

    • Happy to stand corrected on the empirical side! As was probably clear but implicit in my comments I was thinking more of the theoretical side of things.

      I agree 100% that if you interpret “non-stationarity” more broadly and loosely, there are lots of people working on it. Part of what’s going on under the surface in this post is me going back and forth on whether non-stationarity in the stricter sense I discuss in the post is worth worrying about *specifically*. Or whether, for most practical purposes, it’s indistinguishable from from transients, non-equilibrium stationary variability, etc., and so not worth any specific attention.

      • To me the strict definition of stationarity is constant mean, variance and autocovariance.

        So transients and stochastic equilibria (e.g. around a density-dependent equilbrium) can be stationary. But stationarity is not particularly tied to equilibria. you can have stationary periodic or choatic dynamics for example. In my mind stationarity is saying the probability distribution of points visited is constant (I envision a normal curve placed down on an axis of abundances for example). Technically stationarity requires only the first two moments to be constant but does require the autocovariance to be constant, so my vision is not exactly right, but its close.

        Non-stationarity is primarily in my mind synonymous with external forcing – e.g. climate changing due to humans which in terms drives changes in mean and variance of biological systems because the mean and variance of the climate is changing. Hence my leap to include global change under the label of nonstationarity. In principal anytime you have a trend (change in mean with time) you have non-stationarity, although many economists remove simple trends before analyzing for stationarity.

        That’s how its filed in my head anyway.

      • Ok, all that’s what I tried to convey in the post.

        Re: the sources of non-stationarity, yes, external forcing is a big one. I’m unsure if it’s the only big one.

      • It’s really interesting theoretically, but to me it’s like how many angels can dance on the head of a pin. Technically, it is based on “long-term” behavior, which we will never experience, so why worry about it? Other techniques that assume long-term behavior (equilibria, limit cycles) are best seen as sometimes useful approximations over some windows of time and space. As you say, when those are poor approximations, you can study transients numerically.

        Seems like a big problem for a theory of non-stationary dynamics is how to really explore a model. If all you can do is simulate (maybe even solve analytically) the response to a particular forcing function, how do you come to any general understanding? What parameter do you even put on the x-axis of your results graphs?

        It will be interesting to see how this topic develops!

      • @lowendtheory:

        “Technically, it is based on “long-term” behavior, which we will never experience, so why worry about it?”

        Chalk up one vote for “it’s impractical to study long-term dynamics whether they’re stationary or not, so why worry about non-stationarity”.

        I should actually pick your brain about this sometime in the context of phytoplankton and zooplankton dynamics, because we of course have good long-term data on them from many lakes. And those data often look non-stationary–say, species X has a mid-summer spike in abundance every year for a decade, then stays rare for several years, then pops back up again.

      • I’m still caught up in the non-stationarity story. But if non-stationarity, strictly defined, is a fluctuating mean and variance then it doesn’t bother me much because if we understand the system we could still predict the trend in mean and variance. That is, if temperature drives abundance (both the mean and variability) and temperature goes up then the mean and variance will go up …but this doesn’t surprise us. It fits with our understanding of the world. (I don’t want to downplay the technical problems it causes but conceptually it doesn’t bother me) What concerns me (and what I thought you meant by non-stationary when I first read it) is that the important drivers change over time – that temperature used to be the important driver but now it’s something different – that our understanding of the world is only temporary. This is the one that would keep me up nights if I thought about it too much. That the causal driving forces change over time – and that seems perfectly plausible. Jeff

    • I would add to the list of Brian: analysis of non-stationarity in species distributions, invasion ecology, epidemiological systems, succession models, many population models (e.g. fish stocks) …

      Also, there are many modelling approaches with stochastic equilibria, such as patch dynamics or simulation model versions of UNTB – in these cases the system can be globally in equilibrium, but locally they will still be non-stationary, and this is a crucial point for the analysis.

      • Yes, epidemiological systems in which an epidemic takes off and then burns itself out are another good example of a well-studied non-stationary system in ecology.

        Depending on what studies of invasion, succession, and shifts in species distributions under climate change you’re thinking of, these strike me as studies of transients rather than non-stationarity. Unless you prefer to take “non-stationarity” in the broad, loose sense Brian suggests (which is a defensible move).

        “Also, there are many modelling approaches with stochastic equilibria, such as patch dynamics or simulation model versions of UNTB – in these cases the system can be globally in equilibrium, but locally they will still be non-stationary, and this is a crucial point for the analysis.”

        Yes, as the post notes.

  3. Fantastic post. I was wandering about the classic residual analysis in regression models topic. If my residual is stationary, can i call that sort of residual purely stochastic? I mean as a white noise (estationary stochastic) process. If So i wont have autocorrelation problems right?. In the other rand if my residual is non-estationary i think in got some sort of signal whithin it. So there will be problems of autocorrelation!!

    • ” If my residual is stationary, can i call that sort of residual purely stochastic?”

      Yes, classical time series analysis, which is focused on forecasting, often treats residuals that way. The goal is to build a time series model so that your residuals have the statistical properties of a white noise process with zero autocorrelation.

    • No, you can’t assume that just because your residuals are stationary that you don’t have autocorrelation problems. Order p autoregressive (AR(p)) processes are stationary processes (if the roots of the AR polynomial lie outside the unit circle) but by definition such processes are autocorrelated, for example. If you are modelling some time series data, one of the diagnostics of the model would be to check say the autocorrelation function (ACF) of the residuals.

      Conversely, the presence of signal in the residuals need not indicate a problem with autocorrelation. The observations Y may just follow some non-linear function of a covariate in the model, or perhaps you are missing an important covariate or interaction in the linear predictor. Once you have that purely deterministic “trend” or signal in the data modelled correctly, your residuals may turn out to be indistinguishable from a white noise process. But until you fix the model, any diagnostic for autocorrelation would show the residuals as autocorrelated.

      Linear regression models assume observations (conditional upon the model) or equally the residuals, are independent Gaussian random variables with mean = Xb (where b = \beta, the vector of regression coefficients), or = zero if we’re talking about residuals, and the same variance \sigma. There is nothing in the model that makes the observations or the residuals behave that way however.

  4. Leaving nonstationarity aside – as a “biggest understudied topic” I’d nominate the population dynamics of plant-herbivore systems. We know lots about the impact of individual herbivores on plants. We know almost nothing about whether/when herbivores affect or regulate plant populations. In fact, I’ve had manuscripts rejected on the grounds that “insect herbivores don’t affect plant populations, only individuals”, which is a pretty bizarre claim….but it is true that there are very few good studies to test the question. (Perhaps McNaughton’s Serengeti work is an exception here? I have to admit when I write “herbivore” inside my head I think “insect”, but I should admit there are non-insect herbivores too!)

    • Wahey, somebody answering the question posed in the post! 🙂 In fairness to our commentariat, I spent most of the post talking about my own answer, so I’m not surprised that’s what we ended up talking about.

      “We know almost nothing about whether/when herbivores affect or regulate plant populations.”

      Is that just because we don’t know much in general about plant population dynamics? Not much good long-term time series data? Or because we haven’t done the right experiments? Or what? It’s kind of a weird knowledge gap, whatever it is, since plants and many herbivores are so easily manipulable.

      ” In fact, I’ve had manuscripts rejected on the grounds that “insect herbivores don’t affect plant populations, only individuals”, which is a pretty bizarre claim….”

      Yes, that is a bizarre claim. Reminiscent of the notion that competition only operates at small spatial scales, so can’t affect species’ geographic ranges. Neglecting the fact that anything that affects every single individual can surely affect geographic range.

  5. You’ll not be surprised to learn that I’d vote for large-scale, biogeographic patterns (never mind processes) in species interactions. There’s still only a handful of studies that have seriously addressed questions about latitudinal trends in specialization, turn-over of participants, etc., etc.

  6. Hello there,

    I really like your post. Actually never heard about non-stationary systems. But back to the oringial question on understudied topics, I think that an understudied topic are the mechanisms of diversity maintenance from soil communities. I work with soil fungi and I always find myself trying to “adapt” general community ecology theory with my system, but sometimes I am wondering if this is the best way. For example, it is possible to use Chesson´s framework on stabilizing and equalizing factors to explain the high diversity of filamentous fungi in the soil? Clearly most of those theories had plants (or insects) in mind.
    Maybe I am being naive here, but soil fungal are so diverse, dominated by organism with filamentous growth, extremely modular with ephemeral source of resources. So a framework that came out with plants and animals having in mind might not be directly applicable. Maybe I am just being too focused in the natural history of the organisms I am using.

    • I don’t think of Chesson’s ideas has having plants or insects in mind. He started developing his ideas when thinking about coral reef fish.

      Having said that, mapping from the terms of a theoretical model to the biology of a real organism absolutely can be a challenge. For instance, if it’s unclear what an “individual” is, then yeah, it’s going to be hard to even define per-capita growth rate, never mind say anything about long-term average per-capita growth rate when rare.

      But I do think those challenges are surmountable, at least sometimes. For instance, Adler et al. 2006 PNAS is an application of Chesson’s ideas to perennial plants, organisms for which it’s hard to say whether two ramets are part of the same biological individual.

      • Thanks for the correction about the origin of Peter Chesson´s work! And exactly, when trying to empirically test some of these theories to fungi, it is hard to imagine ways to measure per capita growth rate, or even thinking about measuring “invasibility”.

        I am not a theoretical ecologist, but I like the generality it seeks. So, beyond the problem of modularity of organisms like fungi, my concern is the following: are the current theories of diversity maintenance applicable to systems that “hyperdiverse”? And I am talking about diversity levels well beyond that of trees in tropical rainforest.

      • I don’t see hyperdiversity per se as a conceptual or practical obstacle to applying Chessonian coexistence theory. If you can figure out a sensible way to apply the theory to the organisms of interest, it applies just as well to 2 billion species as to 2 species.

        The conceptual and practical obstacle to applying coexistence theory to many “hyperdiverse” microbial systems isn’t their diversity, it’s that it’s unclear what a “species” is for theoretical purposes. For purposes of Chesson’s framework, a “species” is something that reproduces, dies, and moves around at specified per-capita rates (rates which of course will vary depending on species’ densities, abiotic conditions, etc.). If soil fungi don’t have “species” in this sense, then yeah, the whole framework just doesn’t apply. But while admitting I know little of soil fungi, I suspect that there is some sensible way of sorting them into species for purposes of applying coexistence theory, if that’s what you wanted to do.

      • Ha! Thanks! It really gives me material to think about…

      • You’re welcome Carlos. Thank you to you as well, you’ve inspired an idea for a future post–the challenge of figuring out how to apply general theory to particular systems, as seen through the eyes of empiricists. As an empiricist, are there general strategies you can use to help you distinguish real challenges in applying the theory from apparent challenges that actually aren’t challenges?

      • I think that is a cool topic. On the top of my head, I would say a strategy is just getting more familiar with the models, I mean what exactly are the parameters included and what are the predictions. This either by self-learning or by coupling with a theoretician. I would say that In my field (BUT I am new at this business) there is a lack of understanding of what parameters to measure if we were aiming at testing general community ecological theories with our systems.

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