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).