Marquet et al. on theory in ecology

Marquet et al. (2014) is a very interesting new paper on theory in ecology–what theories are, why they’re valuable, and what makes for a good one (or a bad one–we’ll get to that). It’s explicitly philosophical, which is great–scientists should be be explicit about their philosophy of science. But it’s also very concrete–Marquet et al. illustrate and support their general philosophical claims with detailed discussions of several familiar ecological theories.

Below are are a bunch of thoughts on the paper (see Peter Keil’s blog for more thoughts). As usual, don’t think of this as “post-publication review”, it’s just me thinking out loud about a paper that’s worth thinking about.

  • Here’s a brief summary of the paper, to whet your appetite and encourage you to click through. Marquet et al. start by adopting the same distinction between theories and models I discussed here. They share my impression that models and data currently are ascendant over theories. They argue that this is bad, that we can’t do without the understanding and unifying general principles provided by good theories. They emphasize the importance of theory-data linkages. They follow philosopher Larry Laudan (1977) in saying that theory evaluation is a comparative matter, and that good theories are “efficient” in the sense of providing more or better explanations and predictions with fewer free parameters. They offer various reasons for preferring efficient theories (which I kinda wish they’d presented in a bullet list, to maximize clarity.) And they discuss examples of efficient and inefficient theories. Their examples of efficient theories: Fisher’s sex ratio theory, optimal foraging theory, the metabolic theory of ecology, MaxEnt, and neutral theory. Their examples of inefficient theories: R* and resource ratio theory, and dynamic energy budget theory.
  • I love that Marquet et al. have the courage of their convictions to criticize some very prominent theories. It really bugs me when people stake out a position but then consciously or unconsciously duck the full implications (e.g., focusing on the upsides and not the downsides). The only way you can evaluate and improve your ideas is by facing up to their full implications.
  • And I do think it’s fair to read Marquet et al. as criticizing some theories. They say that “Our strategy is not normative”, but I think it actually is. They don’t merely describe what efficient theories are, they talk at length about why theories should be efficient. Now, they recognize the value of other things besides theories, and other virtues of theories besides efficiency, and maybe that’s what they mean when they say they’re not being “normative”. But make no mistake, they think theoretical efficiency is really valuable and that inefficiency is a significant strike against a theory, even if that strike might be counterbalanced by other things.
  • I don’t agree that theory evaluation should always be a comparative matter. If all of our current theories about X are bad in some absolute sense, I think it behooves us to recognize that, rather than just sticking with (and trying to improve) the best apple of a bad bunch. And no, this doesn’t necessarily mean making the best the enemy of the good (or good enough), or giving up on the possibility of incremental improvement of inevitably-imperfect theories. Indeed, one important spur to the development of new, better theories of X is recognizing the inadequacy of all current theories of X.
  • In passing, Marquet et al. make many remarks with which I agree. Theories mostly aren’t very useful unless they’re expressed mathematically. All theories make simplifications and so are literally false, which is what makes them useful. Theories are valuable for other reasons besides making predictions. Just because a theory leaves lots of unexplained variation doesn’t necessarily mean it’s bad. Etc. Many of these points are familiar, but I liked seeing them all made in one place.
  • I’m sure there’s a lot more that could be and has been said on the philosophical side here (and I’m not the one to say it, because I’m not a philosopher, I just play one on the intertubes). Larry Laudan’s work is very influential, but is far from the last word. Still digging a bit for good overview links (will update the post if I find any), but it’s hard because there’s a big philosophical literature on issues like simplicity and unification.
  • Following on from the previous bullet, there are tough philosophical issues here to do with “explanation”. Marquet et al. want theories that explain why the world is the way it is. I want that too. But it’s not always obvious what counts as “explanatory” (see here and here for some discussion). For instance, MaxEnt provides explanations in terms of “constraints”. Given the constraints (e.g., that you have X species, and that mean abundance per species equals Y), it tells you that the species-abundance distribution (or whatever) will be the smoothest distribution consistent with those constraints. But what if those constraints aren’t exogenously determined? What if they’re endogenous, determined by the same underlying forces that also determine the things MaxEnt is trying to predict? Is MaxEnt then “explaining” the things it predicts? Or is it merely showing that the constraints and the things it’s trying to predict are correlated? Or maybe it’s neither, maybe MaxEnt is just pushing the explanatory question back a step, to “What explains the values of those constraints?” Honest questions, to which I’m unsure of the answer.
  • Marquet et al. makes for a really interesting contrast with Evans et al. (2013), another recent paper on theory in ecology. For instance, Evans et al. argue that complex models are more general than simple ones (though I think they mean something different by “general” than Marquet et al.). They argue against the idea that simplicity has a single definition. They argue that simple models aren’t explanatory (for the record, I disagree). They even argue that it’s currently more difficult to publish system-specific modeling work than it is to publish general theory (I disagree with them on this too, at least if we’re restricting attention to general ecology journals, unless they’re just thinking of some very particular sort of modeling like individual-based simulations). So if you want a provocative pair of papers for your lab group or reading group, something to really get people thinking and talking, you should totally read Marquet et al. and Evans et al. (and then comment to tell us how the discussion went!)
  • It’s striking that several of the theories Marquet et al. call “efficient” are macroecological. It’s interesting to ask why that is. Maybe it’s just happenstance. Or maybe certain kinds of problems are more open to theorizing about (e.g., problems characterized by statistical symmetries)? Whereas others demand models rather than theories (e.g., questions about population dynamics or species coexistence)?
  • Marquet et al. think it’s essential to link theories to data, and so in that respect contrast with folks like Caswell 1988. Indeed, they almost leave the (accidental?) impression that what they really care about is not efficiency or generality or fundamentalness of theories, but how easy it is to test the theory. Unfortunately, they don’t talk much as I’d have liked about the effectiveness of empirical tests. For instance, empirical tests of neutral theory often have been uninformative (McGill 2003, 2006). But that might change in future, as it seems to be for MaxEnt (White et al. in press).
  • More broadly, how many times a theory has been tested, and in what ways, and how informatively, depends on not just on the theory’s efficiency but also on all sorts of other factors. I don’t know that Marquet et al. would deny that, but they sometimes give the impression that they think it’s the theory’s fault if the theory hasn’t been tested a lot.
  • Which leads to my biggest disagreement with the paper: their criticisms of R* theory and dynamic energy budget theory. I was very surprised by these criticisms, but tried my best to think hard about them because the paper as a whole is quite good and because the authors are all really smart, thoughtful ecologists. But having thought hard about it, I still think Marquet et al. are off base. They say R* theory is difficult to test because you have to measure at least three parameters for each competing species in order to test it. Sorry, no. I know this because I’ve tested it myself in experiments that involved measuring one parameter per species, namely R* values (Fox 2002). So have other people (e.g., Harpole & Tilman 2006). And if you say, well, that’s still one parameter per species, which is still a lot because after all there are lots of species in the world, well, I don’t see why that’s so different than tests of the metabolic theory of ecology or MaxEnt or neutral theory. For instance, testing even one allometric scaling exponent predicted by metabolic theory requires measuring two numbers (body size, and whatever you’re regressing on body size) in hundreds of species of widely-varying sizes. Yes, all those numbers get boiled down into an estimate of a single parameter–the allometric scaling exponent–but that doesn’t thereby make metabolic theory easy to test. Similarly, MaxEnt predicts various things based on just a few “constraints” like mean abundance per species–but to measure those constraints you have to measure various properties of all the species and then take their averages. And that’s before we even talk about how there are often ways to test theories that don’t involve “estimating all of their parameters”. So whatever the virtues of efficient theory might be, “reducing the number of things you have to measure in order to test the theory, thereby making the theory easier to test” is not one of them. Marquet et al. also complain that R* theory has mostly been tested with small organisms (or grassland plants, they might have added). True enough–that’s because those are the species for which R* values are easiest to measure (though not easy in an absolute sense). But why is that relevant? Doesn’t that amount to implicitly giving neutral theory, MaxEnt, and metabolic theory “extra credit” for the fact that body sizes, abundances, and metabolic rates often are pretty easy to measure or estimate, so that lots of people happen to have measured those things on lots of species already? Surely neutral theory, MaxEnt, and metabolic theory shouldn’t be given “extra credit” for having parameters that happen to be easily measurable or estimable. Any more than one should ding general relativity or the Standard Model of particle physics for having parameters that require expensive high tech equipment to measure. And I’ve tried, but I just cannot understand why Marquet et al. see empirical and theoretical work on optimal foraging theory as an example of efficient theory and strong theory-data linkages, but see R* and resource ratio theory as an example of inefficient theory and weak theory-data linkages. Because to my mind the two bodies of work are very similar in what sort of theories they are, the ways in which people have tested them (e.g., by measuring species-specific parameters), the fact that they’ve both been tested mostly with certain kinds of organisms, how they’ve been modified and extended to incorporate realistic complications to the simplest limiting cases, etc. Compare Grover (1997) on R* theory and data, and Stephens and Krebs (1986) on optimal foraging theory and data–is there really a world of difference there? Finally, I think it’s worth considering effectiveness of tests here too. Tests of R* and resource ratio theory might be hard to conduct, but I don’t think it’s an accident that most of those tests have been really good tests. One nice thing about a theory being hard to test is that it prevents bandwagons based on weak tests of the theory. As far as I know, nobody’s ever seen an opportunity for a quick paper in testing R* theory. So if you’re going to count number and diversity of tests against R* theory, shouldn’t you count quality of tests in its favor? I know much less about DEB theory (though I do know a bit), but I suspect similar remarks would apply. (e.g., here’s Cressler et al. 2014 linking DEB theory to data on host-parasite interactions in Daphnia).
  • I wish Marquet et al. had been a bit more precise about the various reasons why we might want a “simple” theory. For instance, a simple theory might define a limiting case which we hardly ever observe in nature (not even approximately). The “R* rule” and various optimal foraging theorems (“0-1” diet rule, ideal free distribution) are examples. The point of such theories is focus attention on a factor of interest, whether or not that factor is more “important” (by any measure) than those omitted from the theory. Another seemingly similar but actually quite different way a simple theory can be helpful is by including the most important factor while omitting less important ones. Metabolic theory is an example–if you want to explain metabolic rates, the two most important things to know are body size and temperature. Both sorts of simple theories can be described as providing a “baseline” that helps you learn something about the factors omitted from the theory. But what you learn from such “baseline” comparisons is different when the “baseline” is an unrealistic limiting case, vs. when the “baseline” is realistic in the sense of including the most important factor. The former is a conceptual baseline, the latter is an empirical baseline. Evans et al. make this point too (their “demonstration” models are what I’m calling theories of simple limiting cases).
  • The previous two bullets illustrate how tricky it can be to apply general principles (here, general philosophical principles) to specific cases. I think the previous two bullets also illustrate a point from the philosophy of science literature: “simplicity” is an infamously slippery concept, and it’s infamously difficult to say why scientists should prefer “simpler” theories. This is something I’ve talked about before in an ecological context. See Evans et al. for further discussion.
  • Following on from the previous bullet, it’s interesting to try to put other examples into Marquet et al.’s framework. For instance, is island biogeography theory efficient or not? Metapopulation theory? Life history theory? The point of such an exercise is not to slap labels on theories, but to try to come to a better comparative understanding of what works and what doesn’t in theory development. And I’m curious how Marquet et al. would’ve looked different if it had been written by people who believe in the same general philosophical principles, but who’ve developed different theories (among the authors of Marquet et al. are people who’ve worked on several of the theories Marquet et al. praise, but not the ones they criticize). For instance, in a 1987 paper Dave Tilman himself argued for R* theory as a simple, general theory based on a small number of fundamental parameters that makes testable predictions about lots of different things, facilitating tight linkage of theory and data. So, pretty much all the same general points as Marquet et al.–but the opposite illustrative example!
  • Nitpicky aside: what is “the” metabolic theory of ecology, exactly? Is is really one theory, or is it better thought of as a whole complex of different models or theories that all involve body size and metabolic rate? Don’t misunderstand, I can totally see that metabolic theory is an integrated body of work, and it’s totally fine to refer to that body of work as “the metabolic theory of ecology”. But if you’re trying to rank theories by their efficiency and defining efficiency in terms of number of free parameters, well, what’s the total parameter count for the entire complex of ideas that together comprise the metabolic theory of ecology? I bet it’s pretty high (e.g., there’s a whole bunch of parameters just in the original West et al. 1997 paper). One could of course ask similar questions about other examples Marquet et al. raise.
  • Marquet et al. talk briefly about theories as unifying, but they miss that there’s more than one way to have unification. One way to get unification is to have a single fundamental theory that explains a lot, at least to a first approximation; that’s the sort of unification Marquet et al. have in mind. But another way to get unification is to have general theoretical frameworks that, while not making any testable predictions themselves, bring together lots of different system-specific models under a unifying umbrella. Modern coexistence theory as developed by Peter Chesson and colleagues is a prime example of this sort of unification in ecology, and the Price equation is a prime example from evolution. More broadly, see here and here for discussion of how having a bunch of system-specific models is not the same thing as just having a disunified “stamp collection” of unique special cases. Of course, those are two different senses of “unification” and there’s probably an interesting discussion to be had about whether one can substitute for the other (my tentative view is that they’re at least partially substitutable). I talked more about this in one of the first blog posts I ever wrote (and still one of the best, I think).

12 thoughts on “Marquet et al. on theory in ecology

  1. Great blog! I had a pretty similar reaction to the article, specifically, on the criteria for an efficient theory.

    For one thing, I think it is important to keep in mind different theories try to explain different processes, and therefor comparing two theories on the basis of the number of free parameters may not always be sensible. By nature, theories of macro-ecological patterns can generally ignore a lot of detail, which in other contexts are incredibly important.

    I also wonder what makes the metabolic theory of ecology an efficient theory, rather than just a useful empirical relationship? The way the section on MTE theory was written, it would see like the authors would consider MTE theory efficient regardless of whether or not the initial mechanisms proposed for MTE theory are valid. You don’t need the assumptions of MTE to be correct to use empirical body size scaling relationships to make predictions about ontogenetic growth, population growth rates, and community structure. In fact, there are quite a few theories that predict similar scaling relationships, does that mean they are all equally efficient? It has been relatively easy to test MTE’s predictions for how metabolic rate should scale with body size (although most recent work has not supported the idea of a universal scaling law; see review by Glazier 2014). However, testing whether this pattern is due to the mechanism proposed by WBE has been much more difficult to test, and those tests have often not supported MTE theory (Apol et al 2008, Hirst et al. 2014). The challenge for ecologists is figuring out if these mismatches should be interpreted as context-specific deviations from baseline predictions to be expected from any general model, or that we have the wrong mechanism and need to search for a more efficient theory.

    Apol, M. E. F., Etienne, R. S., & Olff, H. (2008). Revisiting the evolutionary origin of allometric metabolic scaling in biology. Functional Ecology, 22(6), 1070-1080.

    Glazier, D. S. (2014). Metabolic scaling in complex living systems. Systems,2(4), 451-540.

    Hirst, A. G., Glazier, D. S., & Atkinson, D. (2014). Body shape shifting during growth permits tests that distinguish between competing geometric theories of metabolic scaling. Ecology letters, 17(10), 1274-1281.

    • Hey, a comment! And not just a pity comment from Brian or Meg (which is what I was expecting after a full day of no comments), but a really good comment!

      Great point re: the efficiency of a theory needing to be judged relative to the sorts of things it’s trying to explain or predict. Which gets into interesting and challenging issues, because in the absence of a theory I think it’s hard to say what sorts of problems can be attacked with low-parameter models vs. high-parameter models. And that’s before you get to what sorts of problems can or can’t be unified by the same theory. For instance, until Darwin came along I don’t know that it was obvious that development/embryology, biogeography, paleontology, and animal husbandry had anything to do with one another. It’s a bit like trying to say how many “niches” there are in the absence of any species occupying those niches. Wish I knew if there was any philosophical work on this issue.

      Really good question re: the MTE just being empirical relationships rather than a theory. I deliberately avoided that in the post because I was afraid I’d be kicking a hornet’s nest if I raised it. But since you’ve kicked the nest first, I’ll kick it too. 🙂 I’m far from an expert on MTE, but I share the impression that it’s mostly just showing how different allometric regressions are all mutually consistent, with the main (only?) theoretical-explanatory bits being the circulatory system optimization stuff. And I share the (admittedly cursory) impression that the jury is very much out on whether those explanatory bits are right. Both because of potential issues with the derivations, and with the resulting predictions.

      The issue of distinguishing between a model that’s basically right but omits some details of secondary importance, and a model that’s basically wrong (giving the right predictions for fundamentally incorrect reasons), is a really important one. Also a really challenging one in many cases, including with MTE.

    • p.s. Thanks for the link to the Glazier review, that’s very interesting reading. Quite a sobering assessment of the mechanistic foundations of MTE. I suspect the whole MTE research program could serve as a good case study for some historian or philosopher of science interested in how scientists go about testing theories, modifying them in light of tests, deciding what data count against a theory, deciding what tests would be most informative, etc. Because when it comes to MTE (and competing theories), scientists have disagreed about all those things.

      EDIT: Also, I wonder how aware ecologists (as opposed to physiologists, zoologists and botanists, life history folks, etc.) are of all the debate about MTE that Glazier reviews. And it’s not just MTE, you could ask similar questions about lots of ideas in ecology that are of wide interest, but which are deeply studied by many fewer people. In general, I think it’s interesting to ask about how the views of specialists on any topic differ from the views of those who are only passingly familiar with the topic…

      • There have been quite a few papers recently that have focused on identifying the types of experiments that would differentiate between alternative theories of metabolic scaling (other than just using more data to look at the same patterns that originally motivate the theories; e.g. is the slope closer to 2/3rd? or 3/4ths?):

        Kearney, M. R., & White, C. R. (2012). Testing metabolic theories. The American Naturalist, 180(5), 546-565.

        Price, Charles A., et al. “Testing the metabolic theory of ecology.” Ecology Letters 15.12 (2012): 1465-1474.

        And now it seems like some of the types of tests suggested by these papers are starting to show up in the literature:

        Hirst, A. G., Glazier, D. S., & Atkinson, D. (2014). Body shape shifting during growth permits tests that distinguish between competing geometric theories of metabolic scaling. Ecology letters, 17(10), 1274-1281.

        Sears, Katie E., et al. “Ontogenetic scaling of metabolism, growth, and assimilation: testing metabolic scaling theory with Manduca sexta larvae.” Physiological and biochemical zoology 85.2 (2012): 159-173.

        White, Craig R., et al. “A manipulative test of competing theories for metabolic scaling.” The American Naturalist 178.6 (2011): 746-754.

        It is difficult to keep up with work on metabolic scaling theories. I have a sense that the majority of those that work on this topic are slowly starting to shift away from thinking that a universal transport mechanism explains patterns of metabolic scaling (although this is just my impression). However, because most ecologists don’t work on this field directly, I think this shift might take a long, long time. I think MTE is particularly attractive, because although the maths used to generate the scaling relationship are somewhat complex, using the relationship predicted by MTE theory is incredibly easy. Also, regardless of what mechanisms brings about an approximate 3/4 scaling relationship, it is an extremely useful empirical relationship to use to address big questions in population and community ecology. It is interesting though that not nearly as many people were making use of this empirical relationship until MTE theory came around. I think what this shows, is that deep down, we all really want simple models, based on first-principles, and are much more excited to use an empirical relationship when we think we have a universal, mechanistic explanation for it.

      • @ Benjamin Martin:

        “Also, regardless of what mechanisms brings about an approximate 3/4 scaling relationship, it is an extremely useful empirical relationship to use to address big questions in population and community ecology. It is interesting though that not nearly as many people were making use of this empirical relationship until MTE theory came around. I think what this shows, is that deep down, we all really want simple models, based on first-principles, and are much more excited to use an empirical relationship when we think we have a universal, mechanistic explanation for it.”

        That’s a *great* point, I think it’s right. And if it is, it’s kind of strange in a way. I mean, if all you need for your own work is the empirical relationship, why do you need to know the first principles-based, mechanistic explanation for that relationship? Or even need to know that there is or might be such an explanation? Why do you care? I can imagine various good reasons why you would care (e.g., you might want to anticipate when the relationship will break down). But it’s a little strange to think that among those reasons would be “Now it’s ok for me to make use of this empirical relationship, because now there’s a mechanistic explanation for that relationship.”

        This old post on Steven Frank’s work is relevant here ( So is the philosophical idea of “screening off”.

  2. I really enjoyed the paper and your discussion of it, Jeremy. I got the impression, similar to Benjamin I think, that the reason for preferring some theories over others is in a preference for macro-ecology. The way I read the dismissal of resource ratio theory is that it requires a lot of parameters to predict e.g. SADs or latitudinal diversity gradients. I am not sure that’s fair, because actually the theory is meant to explain more specific, local phenomena, like local co-existence. Perhaps you should try to unify as much as possible, but could it not also be true that you can get away with ignoring parameters at different levels of integration, meaning that none are more fundamental than others? A meteorologist would use even fewer parameters to describe the biosphere and see no use for more deliberate models, hence rendering them inefficient for her purposes.

  3. Eric Charnov emailed me the following comment, which I’m posting with his permission (he ran into some technical issues with WordPress):

    “Sex ratio theory is not very precisely described in the paper, so the message may be lost.

    Sex ratio ‘theory’ is based upon one great inheritance symmetry: everyone has one mom , one dad [ male and female contribute equally to zygotes]. This clearly refers to autosomal genes….. sometimes this symmetry is violated [ sex linkage, cytoplasmic inheritance, etc] with often extreme results for natural selection on the sex ratio. RA FISHER used this idea in a very clever new way in 1930, but the idea actually predated him. If we combine this with normalizing selection models [ really ,ESS models: this is frequency dependent selection ] we can predict all sorts of things about dioecious sex ratio. Then we generalize, to haplodiploidy , and further to simultaneous hermaphrodites and sex reversers; the first extends the symmetry principle, the latter uses it in new systems, where we now see, for example, allocation to pollen vs seeds in hermaphroditic plants in a new way. While we have some dynamic tests of the theory [ move pop sex ratio away from the equil, let selection do its stuff, and see if it moves back: hint.. it does], most predictions are of the normalizing selection ,or ESS, values. Some of these are surprising, and lots are correctly predicted. More ecologists ought to learn it. Yes, its is an efficient theory.”

  4. The specific goals and objectives of ecologists are heterogeneous in the extreme. An individual ecologist might be interested in explaining or predicting any number of things: how animals make decisions, why populations cycle, the community-level consequences of global warming, why diversity declines with nutrient addition, how increase CO2 influences C and N cycling, etc.

    Coming specifically from the point of view of community ecology, I wonder if starting with the goal of efficiency might result in a body of largely macroecological and mathematical theory that may well have few assumptions and free parameters, but that doesn’t actually pertain to many of the things people want to predict or explain in the first place. For example, I have never found reason to draw on MTE or METE to help explain or predict things that are of interest to me (and many others), such as which of many similar-sized species (e.g., trees) will increase or decrease in abundance in response to warming, whether anthropogenic disturbances will cause biotic homogenization, or whether biotic interactions can constrain geographic range shifts. I have seldom been interested to predict the slope of a species-area relationship or the shape of a relative abundance distribution, nor have park managers I interact with indicated any interest in such quantities. This is just one person’s experience, but I doubt that I’m alone.

    I have great admiration for the theories touted for their efficiency in this paper, I have drawn on some for inspiration myself, and I think they represent profound scientific achievements. But let’s not forget to keep in mind what the broad sweep of ecologists, conservationists, managers, and the general public are interested in explaining and predicting to begin with. We don’t want our theories to unwittingly define what we ought to find worthwhile of study.

    • But perhaps we *wittingly* want them to define that? Like, is the problem supposed to be that our theories are defining what’s worthwhile to study, or that they’re only doing so unwittingly?

      I think an important consideration in deciding what’s worthwhile to study is “do we have good theory about it?” That’s not the only consideration, or always a decisive consideration. But it’s definitely an important consideration.

  5. Pingback: Poll results: what are the biggest problems with the conduct of ecological research? | Dynamic Ecology

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