The Folk Theorem of Alternative Hypotheses In Ecology

A folk theorem is a theorem that’s too informally stated to be proven true, and might not even be strictly true, but that nevertheless often seems to hold. For instance, here are the folk theorems of game theory. And here’s Andrew Gelman’s folk theorem of statistical computing.

Here’s my Folk Theorem of Alternative Hypotheses In Ecology. Imagine you have several reasonably plausible alternative hypotheses about how ecological variables X and Y will be related.* Some or all of your hypotheses make different predictions about the the X-Y relationship (e.g., one says it’s humped, another says it’s an increasing linear relationship, etc.). But you have little or no data on how X and Y actually are related. Or maybe there is a lot of data, but it’s scattered throughout the literature and so no one knows what it would show if it were compiled.** Then my folk theorem says that none of those predictions will hold in a substantial majority of the cases, and there will be no rhyme or reason to which prediction holds in any particular case.

Shorter folk theorem: if anything can happen in ecology, anything will happen.

Example: the intermediate disturbance hypothesis. Ok, there’s actually not that much mathematical theory predicting diversity-disturbance relationships (as distinct from verbal arm-waving, which doesn’t count). But what theory there is makes predictions that are all over the map. Change the model structure, or even just change the model parameter values or the diversity metric, and you predict totally different diversity-disturbance relationships–humped or linearly increasing or curvilinear or whatever (Wootton 1998, Buckling et al. 2000, Shea et al. 2004, Miller et al. 2011, Svensson et al. 2012). Which according to my folk theorem is why all sorts of different diversity-disturbance relationships are found in both observational data and in manipulative experiments, with no one particular qualitative form of relationship predominating (Mackey and Currie 2000, Shea et al. 2004, Svensson et al. 2012, Fox 2013). There are equally good reasons to expect just about any disturbance-diversity relationship, which is why many different diversity-disturbance relationships occur with appreciable frequency.

A second example: local-regional richness relationships. You can get either linear or concave-down (“saturating”) relationships between local species richness and the species richness of the surrounding region, just by tweaking the parameters of a dead-simple model (Fox and Srivastava 2006). And in nature linear and saturating local-regional richness relationships are about equally common, and there’s no rhyme or reason to when you see one or the other (see this old post for discussion and citations).

My folk theorem is the converse of Steven Frank’s (and others’) notion that simple patterns emerge in ecological data when there are many different processes or mechanisms that would generate the pattern, and few or none that would generate any other pattern. Think for instance of the fact that most every species abundance distribution is lognormal-ish in shape, with many rare species and few common ones. That’s presumably because a lognormal-ish species-abundance distribution is hard to avoid. As illustrated by the fact that most any plausible model of community dynamics, (and many implausible ones) predict a lognormal-ish species-abundance distribution. Contrast that with my folk theorem. My folk theorem says that, when different process or mechanisms all generate different patterns in data rather than all generating the same pattern, you won’t see a pattern at all. Rather, the data will vary idiosyncratically from one case to the next, thanks to case-specific variation in the details of underlying processes or mechanisms.

My folk theorem is consistent with how theoreticians go about their work. Theoreticians either develop their models to explain existing data, or to answer a hypothetical question: what would the world be like if [list of assumptions] were the case? There’s no reason to expect (or want!) the latter sort of model to describe the way the world usually is. And the former sort of model will only describe the way the world usually is if the existing data describe the way the world usually is. If the existing data just comprise a couple of suggestive case studies, or a “stylized fact” that might not actually be a fact at all, theory developed to explain those data isn’t likely to hold more broadly. After all, how common is it for the first few published examples of anything in ecology to turn out to be typical examples? Not that common, right?

What do you think? Is my folk theorem valid? Can you think of other examples? Can you think of counterexamples–maybe even enough so that it should no longer be regarded as a folk theorem? Looking forward to your comments, as always.

*Roughly equal plausibility of the alternative hypotheses is a key assumption here. You can always dream up some reason why anything would happen in ecology. But you can’t always dream up a plausible reason.

*Thus, my folk theorem doesn’t apply in cases where many different hypotheses are proposed to explain a known, well-established pattern in empirical data. The fact that there are seventy bazillion hypotheses to explain the latitudinal species richness gradient is not a counterexample to my folk theorem.

 

17 thoughts on “The Folk Theorem of Alternative Hypotheses In Ecology

  1. Ooh – great post. Lots to engage with here.

    One line of thought I have is I certainly agree about what I think of as statistical limit theorem kind of arguments although yours is not exactly a limit theorem (but statistical laws that make it unsurprising to see something). Mandelbrot talked about this in 1963 when he argues the power law distribution is common because its the only probability distribution that survives 3 types of transformation. Thus in a complex system you can only get noise or a power law distribution.

    I’ve noticed you talking increasingly more about statistical arguments over the years. How do you square this with your strongly mechanistic “its way better science if it has a differential equation” or “its community ecology all the way down” (https://dynamicecology.wordpress.com/2011/05/02/why-doesnt-community-ecology-erase-the-signal-of-historical-biogeography/) roots? Is it a change? Misperception on my part? Or is there a greater whole that unifies these two approaches for you?

    • “Ooh – great post.”

      Thanks! I’m going to assume that all of the very few people who have read it agree with you. 🙂 It’s good that our traffic stats periodically remind me just how “niche” some of my–and your!–interests are.

      “Mandelbrot talked about this in 1963 when he argues the power law distribution is common because its the only probability distribution that survives 3 types of transformation.”

      Ooh, I’ll have to look up that Mandelbrot paper. Steven Frank also emphasizes the importance of the fact that different classes of distribution are invariant under different sorts of transformations.

      “I’ve noticed you talking increasingly more about statistical arguments over the years…Is it a change? Misperception on my part? Or is there a greater whole that unifies these two approaches for you?”

      There’s a greater whole that unifies these approaches. At least in my mind. My old “many roads to generality” post is my attempt to spell it out: https://dynamicecology.wordpress.com/2015/06/17/the-five-roads-to-generality-in-ecology/ tl;dr: I think there are various patterns in ecological data for which the correct explanation is a central limit theorem-type argument. There will be tears before bedtime if you try to explain such patterns with a specific mechanistic model, or try to use such patterns to test alternative mechanistic models. But I think that there are other patterns in ecological data that cry out for explanation in terms of a specific mechanistic model.

  2. Second line of thought you can see how the you will only get one answer approaches (species area relationship has to go up with area, SAD has to be uneven and lognormal-ish) in some way advance science (especially predictive science) even as they make it clear the pattern is not a path to mechanims.

    But while agreeing with you “almost anything can happen in ecology”, how do you see this advancing science?

    • Good question. One answer is, it’s good for ecologists to be more skeptical of “stylized facts”. Don’t be quick to think that just because you found such-and-such pattern in one case study, and came up with one hypothesis to explain it, that either the pattern or the explanation are the general rule. Because with a bit more data collection, and a bit more thought, you could probably come up with contrary data and hypotheses. I think it’s good to try to discover “stylized facts”, and to follow up the ones we do discover with further theoretical and empirical investigation. But I think it’s bad to immediately start treating “stylized facts” as well-established, or as some kind of default baseline expectation. So that contrary data or theory gets held to a higher standard of proof.

      Example: I recall Angela Moles’ old comments here about how she struggled to publish excellent data showing that (by one measure) species interactions were not stronger in the tropics. Reviewers basically refused to believe her data because it was different than previous data. Which was ridiculous because previous data was *very* far from being so voluminous and encompassing to establish “species interactions are stronger in the tropics” as some Universal Law, to the point where we should be suspicious of any contrary data.

      A second answer to your good question is to say that “generality” in the sense of “what happens in most cases” or “what happens on average” is overrated. At least, it’s overrated by some ecologists. It’s not the only sense of “generality” worth seeking. I’d like to see ecologists collectively care a bit less about generality in the meta-analytic sense of “what happens in most cases” or “what typically happens on average”. I’d rather they cared a bit more about generality in other senses.

      • What about generality in the sense of “it goes up 30% of the time, flat 20%, and down 50%”. Or even better “it goes up 30% of the time, mostly in high nutrient systems, flat 20% of the time mostly in dry environments, and down 50%”

      • “What about generality in the sense of “it goes up 30% of the time, flat 20%, and down 50%”. ”

        That’s generality in the sense of a descriptive statistical summary. And I think it’s pretty boring and useless. Boring because it doesn’t teach me anything surprising, and useless because there’s no way to build on it. It doesn’t give theory anything to explain, and doesn’t suggest any useful directions for further empirical work. It’s this sort of summary that I was complaining about in my old post about how meta-analyses often seem to be the (dead) end of empirical research programs. To my mind, if the “end product” of some sustained empirical research program is something like “it goes up 30% of the time, flat 20%, down 50%”, then that program unfortunately turned out to be mostly a waste of time. I think the empirical research program on local-regional richness relationships is an example.

        “Or even better “it goes up 30% of the time, mostly in high nutrient systems, flat 20% of the time mostly in dry environments, and down 50%””

        I suppose that’s a bit better, because there’s a signal in the noise. That suggests that if you condition on one or two key covariates (nutrients and aridity in your example), you can find generalities that would provide a fruitful starting point for further theoretical and empirical investigation. “Why does Y usually/always increase with X *in high-nutrient systems*?” could well be an interesting fact that cries out for (and maybe also suggests) a theoretical explanation that could then be tested empirically.

        But how often do the covariates in ecological meta-analyses in ecology yield those sorts of clear-cut “conditional generalities”? Not often, I’d say. Usually, it’s more like “Y increases with X a bit more often, or a bit more strongly on average, when condition Z holds then when it doesn’t.” That is, the covariates only explain a modest amount of the variation in the X-Y relationship. And further, they’re often not the sorts of covariates on which to build any tractable hypotheses. Think of covariates like “biome” or “continent” or even “terrestrial vs. aquatic”. Ecologists’ attempts to build useful “periodic tables” of variation mostly have not panned out, as far as I know. But then again, maybe I’m just unaware of a bunch of great examples? So maybe that would be a good follow-up post. Ask the readership “Are there any useful ‘periodic tables’ in ecology?” The only one I can think off the top of my head is the association of vegetation type with temperature and rainfall.

      • “To my mind, if the “end product” of some sustained empirical research program is something like “it goes up 30% of the time, flat 20%, down 50%”, then that program unfortunately turned out to be mostly a waste of time.”

        Interesting – I don’t think I agree at all. What do we do with these questions. Just never address them? Just say anything can happen and go no further? To my mind they have just moved from elegant physics-like to messy engineering-like. And there are plenty of reasons to do engineering-like work. And quantifying the proportions lets you quantify other things downstream and make predictions which is kind of the point of engineering-like work.

        “”. Ecologists’ attempts to build useful “periodic tables” of variation mostly have not panned out, as far as I know.”

        Yeah I find this research program fascinating but remain on the fence about its efficacy. MacArthur called for it in 1972 and Schoener called for it in 1986. But examples are hard. Certainly there are interactions (effect of adding nitrogen depends a lot on whether water and phosophorous are abundant or scarce) but that doesn’t quite rise to the “periodic table”.

        I think ecology might be moving towards classifying seems based on whether dispersal is common or rare might be emerging (e.g. Chase & Leibold metacommunity book), but its not 100% formed yet. There have to some that are so obvious that we don’t really think of them as interesting too – e.g. vertebrates tend to have lower population variability than invertebrates. Fire gradients are pretty obvious structures of plant communities in a lot of ways.

      • “What do we do with these questions. Just never address them? Just say anything can happen and go no further? ”

        You tell me–you’re the one who thinks “it goes up 30% of the time, flat 20%, down 50%” is an interesting result that provide a fruitful basis for further research!

        One way to answer your question is to ask what ecologists actually have done when faced with this sort of scenario, and ask how well their choices have worked out.

        Take local-regional richness relationships. We now know that they’re linear about 50% of the time and saturating about 50% of the time (depending on your preferred method of classifying ambiguous cases), with no covariate that explains when you see linear vs. saturating relationships. How have ecologists working on local-regional richness relationships responded to this? As best I can tell, by just giving up and moving on to something else (which I emphasize seems to me eminently sensible–I’m not criticizing anyone here!) Recent perspectives-type pieces from senior researchers in this area involve a lot of handwaving about placing local-regional richness relationships within the broader context of beta diversity and biogeography. Without coming right out and saying so, everybody’s just quietly agreed to give up on asking whether local-regional richness relationships even have a “typical” shape. And it’s been a long time since anybody published any theory inspired by local-regional richness relationship data as far as I’m aware. (EDIT: I personally am not into a broader, redirected research program on beta diversity, but that’s just me; I’m sure others are and that’s fine. I just don’t think that broader, redirected research program on beta diversity really gained anything important in terms of motivation or background information from the local-regional richness research program that preceded it. I don’t see that broader, redirected research program on beta diversity as building on or continuing previous local-regional richness work in any important way.)

        You could say the same for the IDH. Plenty of people still study the effects of disturbances, of course, as well they should. But it’s all system-specific, mechanistic case studies as best I can tell. Studies of, say, conifer forest regeneration following crown fires, or coral reef regrowth following hurricanes, or whatever. Very few people are trying to develop or test general theory about disturbance-diversity relationships, or identify as-yet-undiscovered general patterns in published diversity-disturbance data that might give theory a target to shoot at. EDIT: And I don’t think the many case studies of post-fire regeneration or post-hurricane recovery or whatever really build on or continue the IDH research program in any important way.

        I could keep multiplying examples like this all day. A little while back I saw a meta-analysis of studies of the effects of ecosystem engineers on species richness of co-habiting species. Highly-heterogeneous effects, with no rhyme or reason to the heterogeneity. How are you supposed to follow that up or build on that, besides shrugging and saying “welp, ecology’s complicated, anything can happen”?

        But you tell me–are the examples that happen to come to my mind some very non-random sample of all examples? What are the most productive, most fruitful ecological research programs that have built on data showing something like “it goes up 30% of the time, flat 20%, down 50%”? I ask because I’m not sure what you mean by “engineering-like work”. Some examples would help.

      • Personally I think 30%/50%/20% is a more satisfying endpoint than anything can happen. I don’t think there has to be something additional that comes out of it to justify going to that point. To be extreme anything can happen includes 98%/1%/1%. Sure most people will look at that say that is really Case #1. But what about 60%/25%/15%. Isn’t that more information than “any of 3” while still not going to turn into a general rule of “Case #1 is true”?

        And even if its 30%/50%/20% a more engineering-type example is say you want to estimate carbon fluxes under climate change or richness response to eutrophication. If one is working at the landscape scale one can do a weighted average of 3 responses. And if you only care about one system about which you don’t have knowledge you at least have prior probability.

      • Yes, sure, something like “60%/25%/15%” is more precise and so modestly more informative than “anything can happen”. (But only modestly, I’d say). And it’s not identical to “33.3%/33.3%/33.3%”, so perhaps there might be some interesting reason why the most common outcome is modestly more common than the others (though my money would be on “not” unless the difference in outcome frequencies was extreme).

        And yes, if you need to know a weighted average outcome for purposes of making a prediction, then absolutely, you need to know the weights. I tend not to think about that case because I don’t do that kind of predictive modeling. But that’s just me, obviously.

  3. This is indeed a good question, and I like the notion of a given explanation’s validity if it is induced from a dataset vs deduced from first principles, then tested with same dataset.
    But getting to the folk theorem. I think there is some structure to the chaos of number of possible mechanisms vs number of patterns across systems. Consider the question: What governs the geography of abundance of X? where X is a taxon. If you ask the question of a higher, older, more inclusive taxon, say mammals, birds, grasshoppers, you may begin to converge on a few drivers: productivity, temperature. Ask the same question for each family within those taxa, and the number of potential hypotheses too diversifies. Now imagine the number of mechanisms needed to account for that answer for all the *species* within each taxon….
    There’s a lot of fun stuff going on in the above example that we started playing with in a GEB article back in 2001:
    https://michaelkaspari.files.wordpress.com/2014/12/2001_kaspari_taxonomic-scaling-ants_geb.pdf

    So in evolutionary biology, it might reflect the tendency for evolution—via enough genomes and generations—to converge on similar solutions in the collective via diversification of the individuals in that collective.

    And/or why the behavior of a flask of N2 gas behaves more predictably than the individual molecules.

    Or, perhaps, the more ambitious/general the question,the simpler the number of possible answers.

    • Leave it to a fellow macroecologist to suggest the difference between the Frankian world where one answer is possible the Fox Folk THeorem world where any answer is possible is scale! I agree.

  4. Minor add relative to the rich discussion above.

    A folk theorem (or a folk conjecture, as it’s my own) from computational neuroscience: if you can come up with a biologically plausible mechanism to achieve a computational goal, nature uses it but not in your model system.

  5. Very interesting post. I just want to add that I find the whole idea of a ‘typical’ example to be extremely slippery. In many cases, it feels weird to try to answer ‘how common’ something is when asked very generally. In those settings, I feel that it is better to provide bounds on what is conceptual possible or mathematically consistent and leave the probability distribution over instances out of it. In my case, I am especially concerned about people who generate fitness landscapes as a sample from some probability space of possible fitness landscapes. But this applies more broadly.

    I recently heard a good talk by Karen Kovaka about how so many debates in evolution are about the relative frequency of some mechanisms (say: how common is extra-genetic inheritance?). And how these sort of arguments never really get resolved but just peter out. She argues that the usefulness of these debates is not in actually establishing those relative frequencies that are being ‘debated’ about but their long term productivity is in showcasing causal patterns and regularities of phenomena. I think that Angela Potochnik also writes about this.

    It feels related to your Murphy’s law of alternative hypotheses.

    • ” just want to add that I find the whole idea of a ‘typical’ example to be extremely slippery. In many cases, it feels weird to try to answer ‘how common’ something is when asked very generally. In those settings, I feel that it is better to provide bounds on what is conceptual possible or mathematically consistent and leave the probability distribution over instances out of it.”

      I agree, but I think we’re in the minority among ecologists, unfortunately. I bet if you polled empirically-minded ecologists rather than theoreticians, they’d care a lot about which states of the world are most common.

      Thanks for the pointers to Karen Kovaka and Angela Potochnik.

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