Do evolutionary biologists ever complain about the role of mathematical models in evolutionary biology?

Historically, ecology has been characterized by ongoing vociferous debate about whether mathematical theory has any place in ecology, and if so, what that place is. Sharon Kingsland’s history of population ecology, Modelling Nature, is all about this debate from the founding of ecology up through Robert MacArthur. Charles Elton’s mixed feelings about mathematical modeling exemplify this history. More recently, think of Levin (1975), worrying over what he saw as rampant imprecision in ecologists’ use of mathematical models. Think of Simberloff (1981) vs. Caswell (1988). Think of Robert Peters’ A Critique For Ecology. Think of Scheiner’s (2011) complaint that hypothesis-generating models, and empirical papers based on them, are insufficiently common in ecology. Think of Lindenmayer & Likens’ (2011) opposing complaint (echoing the earlier Dayton & Sala 2001) that mathematical modeling (and meta-analysis and data-mining) is crowding empirical and place-based studies out of the ecological literature (aside: L&L’s complaint is baseless). Think of Greg Dwyer’s complaint on this very blog that too many empirical ecologists are wasting their time trying to understand data generated by nonlinear stochastic processes without the aid of mathematical models. Think of Judy Myers’ counter-complaint that the models too often are untestable (aside: I’m with Greg on that). Finally, think of the recent debate over “theory vs. models” in ecology, which is a debate among mathematically-oriented ecologists as to what sorts of mathematical theories models thingies ecology needs. Theoretician Bruce Kendall (2015) reviews theory vs. empiricism debates within ecology over the course of his career.

Here’s my question: why don’t you ever see evolutionary biologists having these arguments? And isn’t a sign of the comparative health of their field that they don’t?

As best I can tell, evolutionary biologists are all on the same page when it comes to the role of mathematical theory in their field. As evidenced (for instance) by the fact that their leading journals actually publish mathematical theory whereas leading ecology journals mostly don’t (a state of affairs that many ecologists don’t like.) Ok, you sometimes see complaints in evolutionary biology that we need a new Modern Synthesis because the one we’ve got purportedly omits developmental biology or macroevolution or a “theory of phenotypic form” or whatever (e.g., Pigliucci 2009). But that seems to me like a rather different sort of complaint than the complaints about theory ecologists have been debating since the founding of the field.

It’s telling that the very fine paper by Servedio et al. (2014) on the uses of mathematical models in evolutionary biology cites many criticisms of mathematical modeling–almost none of them by or aimed at evolutionary biologists. The only exceptions are E. O. Wilson’s infamous Wall Street Journal editorial on how great scientists don’t need to know math (which isn’t aimed at evolutionary biologists specifically) and a lonely 1964 paper by Haldane defending models of “beanbag genetics”.

Am I wrong about this? Can anyone point me to any debates within evolutionary biology, since the Modern Synthesis, over the role of mathematical theory in the field? And if not, doesn’t that say something good about evolutionary biology, and bad about ecology?

p.s. It’s also telling that “conceptual models” and “conceptual frameworks” are much more popular in ecology than in evolutionary biology. At least, that’s my impression–is it yours? As someone who thinks that verbal and diagrammatic “models” and “frameworks” are pretty much always useless (at best), I regard their comparative rarity in evolutionary biology as another sign of the comparative health of that field.

43 thoughts on “Do evolutionary biologists ever complain about the role of mathematical models in evolutionary biology?

  1. To quote from myself (citing someone else): “Population genetics was initially developed as a theoretical discipline, with process-based models derived before empirical data on the frequency and diversity of alleles in real populations were even available to any great extent (Provine 1971)”.

    That led to a coherent set of models using the same few(ish) parameters, covering a broad range of situations. If you pay attention for a semester you can grasp the essentials that stay with you for a career.

    Ecologists started by observing many different things (latitudinal gradient in diversity, food web structure, species-area/isolation relationships, competing species dynamics) and built a zillion different types of model, many of which bear little resemblance to the others, and some of which seemed to be pulled out of the sky (e.g., broken stick). It all seems like fun and games with equations with either little connection to reality or to only a narrow range of situations. And you can spend years unsuccessfully trying to grasp the essentials that might stay with you for a career. So we complain.

    • Yes, the different histories of the fields–ecology with no one founder, vs. the Modern Synthesis driven by a small group of people including several theoreticians (Haldane, Fisher, Wright) came up in old threads.

      But you’ve put your finger on another important point. It’s not just that theoreticians were part of the core of the field from the get-go. It’s the style of model those theoreticians produced: “high level” models that summarize the consequences of lots of complicated, system-specific underlying biology in just a few parameters like “population size”, “selection coefficient” and “migration rate”. You and I would both like to see more ecologists think in terms of such high level models (,

      Of course, if one wants to ask the further question, why did the founders of population genetics think in terms of “high level” models, well, I think you’re back to Darwin. It’s his idea that *every* species evolves, and does so by the *same* mechanism (natural selection).

    • It’s somewhat ironic it’s the field that started with process-based models that now has general theory. Whereas the field that started with general *patterns* (the species-area curve, the latitudinal diversity gradient, pyramids of biomass, etc.) doesn’t. “Pattern-first” ecologists think of themselves as seeking generalities. They often claim that, by starting from a focus on general patterns, general theory will emerge. Jim Brown is one leading advocate of this view. That’s a plausible view, but I think it’s mostly (not entirely) turned out to be false. I think in part because some of the general patterns that “pattern-first” ecologists have cared most about are very “theory-resistant”. The latitudinal diversity gradient is a good example of an empirical pattern about which it’s basically impossible to usefully theorize, because “latitude” is a stand-in for a heterogeneous mix of factors that resist summarization in terms of one or a couple of “high level” model parameters. And in part because, as you point out, whatever model one might build to explain (say) the latitudinal diversity gradient isn’t likely to have anything to do with the sort of model one might build to explain (say) the shape of the species-abundance distribution or the fact that we usually observe pyramids of biomass.

      In contrast, if you start from process-based models, and if those models are specified at a “high” level and so include a complete list of all the high level processes that exist (in evolution: selection, mutation, migration, drift, speciation), you’re naturally led to study *all* and *only* the sorts of phenomena those models predict or explain. Which naturally leads to a unified research program with tight links between theory and data (at least, once it becomes feasible to collect the needed data).

      Ethan White has an old comment here somewhere about how he’s tired of the “pattern first” vs. “process first” debate. And I certainly wouldn’t argue that “patten first” folks are Doing It Wrong. But I do think one drawback of the “pattern first” approach to science is that it does not often lead to generalities of the sort that pattern-first ecologists themselves say they ultimately want.

      Of course, some of the blame for the current state of affairs also can be laid at the feet of ecological theoreticians. Robert MacArthur for instance didn’t do the sorts of high-level models that folks like Fisher, Wright, and Haldane did. So he got a lot of empirically-oriented ecologists thinking about theory–but arguably the wrong sort of theory if what one ultimately wants is a general theoretical framework analogous to pop gen. It’s an interesting exercise in counterfactual history to speculate what ecology would be like today if Haldane, Fisher, and Wright had gotten into ecology, or if MacArthur had studied with one of them instead of with Hutchinson.

      And it’s interesting that the most influential recent attempt to apply evolutionary-style “high level” models in ecology–Hubbell (and Bell’s) neutral theory–both took off, and then foundered, because of the emphasis on using the theory to explain the empirical patterns that ecologists were already interested in. The shape of the species-abundance distribution, primarily. Interest in neutral theory took off quickly because ecologists really liked the idea of a model that could reproduce the patterns they already cared about. But then interest foundered once everyone realized that the species-abundance distribution doesn’t retain much information about the processes that generated it. So an attempt to bring evolutionary-style models into ecology foundered because ecologists care about explaining one pattern at a time. I wonder what would’ve happened if MacArthur had tried to translate pop gen models into ecology back in the 1960s. I wonder if he’d have been able to say “Here’s a family of high-level models that predict lots of different things depending on their parameter values, empiricists should go out and check *all* of those predictions, not just one of them” and gotten people to listen.


  2. I think evolutionary biology has better measurements than ecology, and can do more strong inference experiments. This does not mean its mathematical theory is subsequently simple, but I think it can be tested more convincingly. This leads to better building blocks for addressing further complexity.

    I took a great course in evolution with Doug Schemske and Jeff Conner and, as an ecology student, I was jealous at how novel experiments with genetic tools (and good theory) could reveal such fascinating insights into nature. But… time and again these studies would “hold the environment constant”, which you can rarely do in ecology. Without a constant environment, things get complicated fast.

    • “I think evolutionary biology has better measurements than ecology”

      I’m not so sure about that. Ok, maybe it does now, thanks to gene sequencing. But this difference between fields predates the advent of gene sequencing by decades. Natural selection was long infamous for not being measurable in the field. For instance, Ford and others spent decades trying to measure it in snails and ended up with pretty ambiguous answers.

  3. Just thinking out loud here, but I think some of this difference has to do with the scale of the units under study. In ecology, there are good mathematical models of population dynamical processes, but things get a lot more complicated when one moves beyond populations and pairwise interactions to whole communities. Evolutionary models typically emphasize processes in populations or along historical lineages. By contrast, there’s not really a mathematical model for, say, the explaining the entire tree of life. In both fields, it seems to me there has been some success in taking population-level models based on birth-death processes and applying them to higher-order entities: island biogeography, in the case of ecology, clade structures in the case of evolution.

    • “things get a lot more complicated when one moves beyond populations and pairwise interactions to whole communities. ”

      Hmm…except that, as Mark Vellend notes, it’s ecological communities (at least, the bits comprised of competing species within roughly the same trophic level) that are analogous to populations in evolutionary biology. Competing types with dynamics driven by selection, drift, and migration.

      • I think the analogy between populations and communities may be a source of trouble, especially if it requires assuming everything is driven by competition.

        Let me also emphasize how complicated things can get, both ecologically and evolutionarily, even within a simple flask founded by one strain of an asexual organism, with a precisely known pool of resources and only a single trophic level.

      • “I think the analogy between populations and communities may be a source of trouble, especially if it requires assuming everything is driven by competition. Let me also emphasize how complicated things can get.”

        Yes, but if you’re starting from a foundation of high level theory, those complications become tractable. At least, that’s the hope! But you could be right that one downside of “high level” theory is that certain ways of “complexifying” the theory tend to feel ad hoc or artificial. For instance, if in your high level pop gen model the selection coefficient is one parameter (or one set of parameters), and the population size is another parameter, it can feel artificial and ad hoc to make the selection coefficient dependent on the population size. Even though, if one started with some lower-level model of the ecology of some particular system, I bet it would be hard to write down a plausible low-level model of any system that *doesn’t* result in some sort of correlation between selection coefficients and population size.

        Which I suppose raises the question: it is easier to start with simple high-level theory and then complexify it as the data demand, or start with lots of system- and case-specific low level models and then unify them under some higher level theory? Obviously, it’s possible to do either one, but is one easier to do than the other. This might just be the ecologist in me seeing the grass as greener on the other side of the fence, but I think it’s usually easier to start with simple high-level models and then complexify them. It’s my impression that that’s exactly what’s happening in pop gen these days, as classical mathematical population genetics turns into computational population genomics to deal with the challenges and opportunities presented by the flood of genomic data. Would you agree with that?

      • (No reply button for your latest response, so putting it here.) Yes, I agree with what you wrote, both as a strategy (“start with simple high-level theory and then complexify it as the data demand”) and as a common practice in evolutionary biology, especially on the pop-gen side of that field (“classical mathematical population genetics turns into computational population genomics to deal with the challenges and opportunities presented by the flood of genomic data”).

        Regarding your point about selection coefficients perhaps depending on population size or density, I also agree with that. Indeed, that’s the sort of place where I think there are many important opportunities is to use ecological thinking to inform understanding of evolutionary dynamics. For example, some of my work with Bruce Levin on bacteria-phage interactions:
        and our work in the long-term evolution experiment on selection on demographic parameters
        and cross-feeding interactions based on metabolic byproducts

        Indeed, while genomics (as you mentioned in another reply) has been a boon to evolutionary biology, including experimental evolution with microbes, I think that a lot of the growth of experimental evolution with microbes comes from people who are interested in understanding and modeling the ecological (as well as genetic) processes (competition, predation, cooperation, demography, etc) that underlie evolutionary change.

      • Daniel — I’m impressed that you knew about and remembered that review! It fits, I think, with Brian McGill’s points about the tension between micro and macro perspectives in both ecology and evolution.

  4. Speaking from someone on the fringe of ecology (mathematics), I wonder if the ubiquitous agreement about mathematics in evolutionary biology leads to some kinds of stagnation, where a field with less set beliefs is more able to adapt to new ideas/approaches. You mention disagreements about the Modern Synthesis, but the impression I’ve gotten from some papers is that people are far *too* married to the mathematical frameworks underlying evolution with respect to the Modern Synthesis. Specifically, Gaussian processes and “white noise” kinds of random processes are very successful because they are reasonable approximations, and very amenable to argument and analysis. These sorts of mathematical ideas underlie a huge amount of evolutionary biology, at least as far as I can tell. But changing these requires changing fundamental assumptions which are ubiquitous in the field, and from what I can tell actually doing this has been a slow process, because it involves redoing/solving old problems in new ways, which seems kind of difficult and fruitless.

    Likely my understanding of these things is pretty vague, and possibly plain wrong, but here are some things which I’ve seen which have given me this impression. (really this is just one response to an article written in response, so reading all of it can give some insight).

    • Hmm, I’m not enough of an evolutionary biologist to really comment. Noble’s stuff, to which you link, seems to me to be another example of the longstanding minority complaint within evolutionary biology of the need for a new Modern Synthesis to add in stuff that the Modern Synthesis purportedly omitted or unjustifiably downplayed. As I said in the post, I tend to see that sort of complaint as rather different than the sorts of complaints that ecologists have about mathematical theory. But maybe I’m wrong about that.

  5. I think this is an apples and oranges comparison. Primarily scales don’t match. Degree of controlled conditions doesn’t match. And types of questions don’t match. So basically I think I’m agreeing with @Telliamead

    The analog of evolutionary theory would have to be population dynamics at which Ricker models, Lotka-Volterra models, etc have been quite successful – in controlled conditions. Which is the analog to evolutionary models. Which I assume you’re happy enough with,Jeremy?

    But in ecology you jump to things like the latitudinal gradient. Totally different spatiotemporal scale. And not coincidentally evolutionists (Dobzhansky, Schemske) have tried to explain this as well. And have produced as few equations and struggled every bit as much as ecologists. Plenty of other examples. Cope’s rule is a pattern evolutionists have tried to understand but not had a lot of success on (and have been down the road of null model wars just like ecologists). If your’e going to look at microevolution you have to compare it to microecology, not micro vs macro.

    I also think you have to recognize the contrast in the ease with which data can be collected. Half of Darwin’s problem getting his theory accepted was that you could only indirectly observe it. You could look at artificial selection changing phenotypes. Or you could look at stratified fossils. But I’m not sure you could say to this day we’ve actually observed an “origin of a species”. Ecologists meanwhile can literally walk out of their house and measure 200 things. Which of course boils down to saying evolution started as a theory about process to explain one basic phenomenon. Ecology started as an empirical inductive exercise about things that point to hundreds of processes.

    • Wait, are you disagreeing with me or agreeing with me? It sounds like you’re agreeing with everything I said, except disagreeing as to whether the comparison is helpful.

      I think it’s a helpful comparison, because I think ecologists could go about their business more like evolutionary biologists. At a minimum, that would involve taking more of a pop gen-style approach to those problems amenable to that approach (I’m just echoing Mark Vellend when I say that). Ecologists taking a more evolutionary-style approach might also mean ecologists devoting less of their collective attention to certain problems (e.g., the latitudinal richness gradient). Instead devoting more attention to problems that, while they might or might not be more tractable, at least have a tighter link to high level pop gen-style theory (and thus a tighter link to one another). But I imagine that suggestion will be controversial, and there’s definitely room for reasonable disagreement on that.

      I also think it’s a helpful comparison because, even if you compare microevolution with “microecology”, there’s *still* a lot more complaining about the role of theory in ecology than there is in evolution. When Judy Myers complains about theory, she’s complaining about population ecology theory and its application to population cycles, not about our struggles to build high level process-based models to explain macroecological patterns. When Dayton & Sala or Lindenmeyer & Likens complain about how mathematical modeling is crowding out natural history, their complaint isn’t specific to population ecology. And Modelling Nature is all about how population ecology models and population ecology experiments conducted under highly controlled conditions struggled to gain wide acceptance. Etc. So I definitely disagree with you if you think the contrast in attitudes towards theory between ecology and evolution would go away if we restricted the comparison to “microecology” and microevolution. Skepticism about the relevance/value of mathematical theory is much more prevalent in population ecology than in pop gen. And that’s what bothers me most.

      Question for you Brian: I get the sense that you think evolutionary biologists collectively have given too much attention to the microevolutionary phenomena that pop gen (and now, population genomics) covers, and relied too heavily on model systems in studying those microevolutionary phenomena? Assuming I’m not misunderstanding you, I’m not sure what to say to that. There certainly is a lot of empirical work in macroevolution that’s not particularly tied to any high level theory (or low level theory). Trying to identify “key innovations” that paved the way for the adaptive radiation of phylogenetic group X, for instance. And I think that’s fine.

      Re: ease of data collection in ecology vs. evolution, I’m just going to stand over here while you debate this with Dan Linden above. 🙂

      • I suppose I’m half agreeing with you.

        I think you’re right that in areas where math is useful, there are more naysayers in ecology than evolution. But I also think that, e.g. people who pursue macroevolution without simple mechanistic models don’t get derided as much as people who pursue areas of ecology unamenable to math do.

        In short I think ecology is more dogmatic and polarized and less utilitarian on the topic of math and that both sides need to take responsibility for that.

      • Judy Myers doesn’t complain about theory but proposes that descriptive models that are not tested with independent field data are not that useful. This is like forming and testing your hypothesis with the same data – a total no no. Interestingly a recent paper from the Dwyer lab states “Previous efforts to explain gypsy moth population cycles have met with limited success” (Paez et al. Am. Nat. 2017). What does this say about the many previous models that did not include disease resistance and had poor fit to empirical gypsy moth dynamics? Were they helpful? Or is this recent work a test of the previous models to show they were not supported by empirical data? In addition they state that “Evidence that the (eco-evolutionary) theory explains cycles in nature, however, is almost nonexistent.”

        Another recent paper by Barraquand et al. Ecology Letters 2017 states “An inclusive theory for population cycles, ranging from ecosystem-level to demographic modelling, grounded in observational or experimental data, is therefore necessary to better understand observed cyclical patterns.” They conclude that progress will be made by feedback between theory and empirical research but an inclusive theory remains elusive. It isn’t clear here again just what aspects of the theory would be tested or if the theory is developed from the empirical work.

        Finally both of these papers talk about eco-evolutionary theory and from this we could conclude that segregating ecological and evolutionary theory is currently unjustified. Furthermore, particularly in population ecology, it is important to not confuse descriptive models with theory.

      • @ Judy,

        Thank you for taking the time to clarify your views. I confess I remain unclear why you think Greg Dwyer’s work is unhelpful. I think we learn something when we build and parameterize a descriptive model including mechanism X (or mechanisms X and Y, or etc.), and then check whether it does or doesn’t reproduced observed population dynamics. Either outcome of that check is informative.

    • @jeremy
      “I think it’s a helpful comparison, because I think ecologists could go about their business more like evolutionary biologists. At a minimum, that would involve taking more of a pop gen-style approach to those problems amenable to that approach (I’m just echoing Mark Vellend when I say that). Ecologists taking a more evolutionary-style approach might also mean ecologists devoting less of their collective attention to certain problems (e.g., the latitudinal richness gradient). Instead devoting more attention to problems that, while they might or might not be more tractable, at least have a tighter link to high level pop gen-style theory (and thus a tighter link to one another). But I imagine that suggestion will be controversial, and there’s definitely room for reasonable disagreement on that.”

      Yeah – but this is the undertone that bugs me. Why should I give pop-gen like modelling (or lotka-volterra modelling) primacy if my questions don’t benefit from it? Should I really abandon my questions to conform to somebody else’s methodological approach? Should macroevolutionists or paleontologists or developmental evolutionists give up their questions to conform to popgen/lotka-volterra style approaches? Should Elinor Ostrom who won a Nobel Prize in economics for her enduring contributions to understanding the complex multi-faceted nature of environmental decisionmaking dropped the topic since it did not have a nice neo-classical equilibrium model? Should engineers stop building bridges and designing airplanes because there aren’t analytical solutions to assymetric stress analyses and turbulent flows?

      I know you’re not a only one correct way to do science person. But I’m not sure how else to interpret this?

      Boiling it all down there are three lines of logic that lead to this popgen/lotka-volterra centric view:
      1) All scientific questions are best-served by using popgen/lotka-volterra style models
      2) Questions that are not best-served by using popgen/lotka-volterra style models are not scientific
      2) Questions that are not best-served by using popgen/lotka-volterra style models are not worthwhile pursuits (on an individual or social level)

      I’m guessing you’re coming from #1 but I really strongly have to disagree.

      • @Brian:

        To clarify: No, I don’t think that we should quit studying any problem that can’t be attacked by pop gen-style models.

        I think that, when a problem is amenable to pop gen-style models, that they ought to be in our toolbox and that if you think otherwise (as some unknown-but-hopefully-small number of ecologists do), you’re wrong.

        I think that Wilson/L&L style blanket arguments against math are bad arguments. I think such arguments get made more often by ecologists than evolutionary biologists, and that bugs me.

        I think that some ecologists are often (*not* always) wrong when they say that documenting empirical patterns (often macroecological ones) is either a necessary or as-good-as-any-other first step towards the development of general theory. I think they’re wrong in part because the sort of general theory those ecologists tend to have in mind tends not to be well-suited to explaining the sorts of patterns those ecologists want to explain.

        I think that ecologists who work in one way on one sort of problem more often tell other ecologists who work in other ways sorts of problems that they’re Doing It Wrong. I think that’s unhealthy for the field, and that it doesn’t seem to happen very often in evolutionary biology. But I don’t have data and you might be right that it’s common in evolutionary biology for pop gen folks to look down on other folks (e.g., macroevolutionary folks) for not working on problems amenable to attack by pop gen-style models.

        Finally (and now I’m finally getting round to addressing your comment!), I can imagine someone making a non-silly case that the collective effort of a field are best focused on those problems, and those systems, on which we can bring the full range of our tools to bear. That other problems are some combination of less interesting and less tractable. I disagree with that case myself, and should’ve made clearer that I do disagree with it (sorry I wasn’t clear about this earlier). But I don’t disagree so strongly that I think the issue can just be dismissed out of hand. “What’s the optimal allocation of individual or collective scientific effort across different problems?” is a really hard question to answer, for all sorts of reasons. But it’s also an unavoidable question that, implicitly, gets answered every day, by our actual individual and collective effort-allocation decisions. And it’s a sufficiently important question that I’m reluctant to answer it by saying that any collective effort allocation that emerges from defensible individual-level effort allocation decisions is equally good. I’m willing to at least entertain the possibility that, collectively, we all ought to give more attention to problem X and less to problem Y than we would do if all left to our own individual devices. And obviously, there are lots of considerations that come into play if we want to talk about optimal collective allocation of effort. One of those considerations might be “is this problem amenable to theoretical as well as empirical attack?” But that’s far from the only consideration. For instance, “is this problem of any direct practical relevance to non-scientists?” is another consideration that comes up often in discussions of the optimal allocation of ecologists’ collective efforts.

        I hope this makes my views clearer.

      • As usual, we agree more than we disagree but the disagreement part is more interesting. I agree that people who attack math when a field clearly benefits from its application isn’t doing themselves or the field a favor. And given that I’ve written blog posts on both the Wilson and L&L you know that I agree there.

        On the third point I’m not so sure. First I don’t agree that pursuit of general theory is a greater goal than pursuit of general pattern. Not sure if you’re saying that or not. As to whether if general theory is the goal, then pursuit of general pattern is not useful, then I get your point but still tend to disagree. Newton sure got a lot of use out of the patterns found by Galileo and Kepler/Brahe and those patterns were all pursued a generation or so before Newton used them to find theory. I think you can move from theory to pattern (paradox of enrichment) or pattern to theory (Lack’s clutch size).

        I’m suspicious of the all knowing scientific optimizer. Planned economies didn’t work out too well and I don’t think planned science would either. You cannot possibly have an optimum until you have agreed goals. Some people’s optimum is going to be defined by understanding, some by prediction. Some by relevance to policy, some by elegant theory, and etc. Science works by individuals who do some combination of pursuing individual interests and meshing those with what society values (in multiple currencies including funding, access to policy makers, etc). This is a very Adam Smith “invisible hand through individual action” view.

        More generally I think tractable and applicable in a complex world are pretty obviously opposites and when phrased that way, I don’t think it is obvious that we can give primacy to one end of the spectrum over the other.

      • @ Brian:

        I share your suspicion of the optimizing central scientific planner, on the same grounds that centrally planned economies didn’t work (though as an aside it’s interesting just how long they seemed like they would work…). I might slightly disagree with you (?) in that I think the “invisible hand” of the “market of scientific ideas” works a little better if the market participants are a bit aware about where the market as a whole is going. If the invisible hand of the market of ideas ends up sustaining some zombie ideas, or to an endless series of trendy bandwagons that get forgotten once they end, or to either an over- or underemphasis on theory, or etc., well, I think it behooves individual ecologists to think about that at least a bit. Market failures are a thing, but in science there’s no government to change the rules of the game to recognize those market failures and prevent those market failures or mitigate their effects. It’s up to the market participants to do that. So if we don’t like the fact that in ecology, but not evolutionary biology (?), there seems to be something of a market for arguments about math, well, is there any way to correct that besides just further individual participation in the marketplace of ideas? (e.g., by writing blog posts telling people that there’s no one Right Way to do ecology) I think the question is at least worth asking, even if the answer is ultimately “no.”

  6. To get back to the question of why ecologists complain about math while evolutionary biologists do not…my additional thought below is a caricature with lots of exceptions (as is the question itself), but here goes with a hypothesis:

    – Many (most?) evolutionary biologists are drawn to the field in part because of the beautiful theoretical/conceptual edifice that pertains to all of life. People with such an inclination tend not to be mathophobes.

    – Many (most?) ecologists are drawn to the field because they love being in nature – they were drawn in literally because ecology seems the antithesis of math/physics within the sciences. The default stance is resistance to math, and if much of the math seems divorced from wild nature, the stance feels justified.

    • I would answer it slightly differently. People value math when it adds value to what they are trying to understand. They don’t value math when it doesn’t add value to what they are trying to understand. People are hostile to math when it doesn’t add value and they feel judged and forced to use it anyway.

      Math adds enormous value to microevolution (and some approaches to macroevolution). It also adds enormous value to physiology, behavior, and population (including two-species) ecology. It is my experience that people that get into these fields are not all a priori math friendly but see the value and spend the time to learn it.

      But to many other areas of ecology I think it would be hard to make a case that math has added much value (beyond statistics and pattern description). I find myself in the odd position of being math friendly but motivated by these kinds of questions where mathematical theory has not added very much. And my career could be summarized as one long trajectory of coming to peace with not letting my math bias get in the way of pursuing the questions that call to me in the best way possible.

      So I think I’m mostly agreeing, but attributing it a little less to philosophical goals and bit more to systems/questions/scales that inspire people.

      • @ Brian:
        “People value math when it adds value to what they are trying to understand. They don’t value math when it doesn’t add value to what they are trying to understand. ”

        So you side with Judy Myers against Greg Dwyer in their old exchange over the value of mathematical models in population ecology? Because they’re both studying population cycles, but only one places much value on mathematical models as a tool. Do you think Judy’s *right* not to value the sorts of models Greg values? Honest question.

        Personally, I do think there are some ecologists who fail to value approaches that would add value to what they’re trying to understand. I wouldn’t venture to guess exactly how common such ecologists are. I don’t think they’re vanishingly rare, and I think they’re more common in ecology than they are in evolutionary biology. But obviously I don’t have any data to go on.

      • No I agree with you. It is hard for me to see how one could say math has little value in population biology, especially cycles. I would have to say those who disagree are iconclasts.

        Such people definitely exist. I don’t have any more data than you do on how common they are. I think you’re probably right that they’re more common than in evolution. Although my somewhat distant and thus less informed sense is that this debate is pretty common within paleontology. And certainly economics has had a bit of an anti-model revolt in the past few decades.

        So probably an equally interesting reslicing of the question is what fraction of those who push back against math are just iconoclasts and what fraction are moving their fields in important directions. That of course is probably highly subjective and difficult to determine even with a good deal of hindsight.

        But in the end I’m just not very concerned about people pushing against math in ecology. Math/theory feels very alive and well in ecology. I actually think say Ecology or AmNat or PNAS publish healthy doses of theory. They don’t publish the stuff where a mathematician adds a term just for fun and then spends three years solving it – those all end up in more specialized journals as they should. But the new theory that is speaking broadly to ecology seems to me to do fine. You’d be hard pressed to look at recent additions to the National Academy and find an anti-math bias as well.

        And as noted above, “pro-math” people do their fair share of harm in ecology in judging people for not using math when it really wouldn’t be meaningful to do so.

      • Could be. Although genomics seems almost like it’s own thing at this point, used as much by molecular biologists to figure out which genes are responsible for X (e.g., biofilm formation in a recent student presentation) as by evolutionary biologists to study adaptation. One can be a “genomicist” in several different fields. That said, I was indeed thinking of evolutionary biology as it was when I was a student.

    • This is a really interesting from a sociological perspective. I feel like academics almost always have bizarre trajectories in terms of their careers (a decade ago I wanted to be a software engineer, and Jeremy and others have commented on the serendipity of their careers as well). Anecdotally, the students I have taught who were studying physics have been much better in mathematics than the students I have taught who were studying engineering. Do these relationships between fields in terms of proclivities to, e.g. mathematics or computation, exist on a wide scale?

      I also feel that many people get a very obtuse impression of mathematics in the American education system, to an extreme degree that many make decisions about what majors to study based entirely on how many mathematics courses they would have to take. This is likely my favourite discussion on this topic, which is worth reading if you are interested in the pedagogy of mathematics:

      • Do you think academics have more bizarre trajectories than other fields? When I was in grad school, the other Ph.D. students in my lab included a prominent herbalist who wanted to learn more about the science behind plant diversity and pharmacology, a former musician, and software developer who got a second bachelor’s degree to pursue biology, although my own trajectory has been quite linear. But other fields are full of interesting people with unique backgrounds. A professor at my undergrad institution quit to start an organic farm; a friend of mine just left her job/career in the education department of an art museum to join the clergy; you hear about entrepreneurs that never thought they would go into business but they had an idea that took off; I often wonder if my future will take me out of science to pursue other interests. I’m not disagreeing with you; of course I have no data, and actually don’t even know my own opinion on the subject. Just posing the question because I think its interesting to consider. If there is a relationship among proclivities to different fields, I wonder if it tracks with the influence different fields have on one another. For example the methodological influence of astronomy on evolutionary biology by the development of bayesian MCMC tools. Or Pearse et al 2017, is a recent example of applying a mathematical tool (“statistical estimators”) to predict phenology solely from occurrence data, which previously had been used by paleontologists inferring extinction timing, and geologists studying earthquakes.

        I definitely agree that the way math is presented in the American education is really polarizing, and also not representative at all of the actual field of mathematics (read: way more narrow than).

      • If I recall some recent data from the NYTimes correctly, academics are more likely than people in most other professions to have at least one parent who was an academic. But the percentage isn’t that high in an absolute sense–only a fairly small minority of academics have parents who were academics.

        Anecdata: Meghan and I both had traditional linear career paths into academia. But Brian did not. After his undergrad, he spent years working at software companies, getting up to some pretty high level positions. Then he decided he’d rather be an ecologist and went to graduate school.

        I have no idea if “nonlinear” career paths are more common for academics in some fields than others. Could be.

    • I have often thought that ecologists are ecologists because they are fascinated by contingencies (consider their infatuation with statistical interactions). This does not bode well for ‘laws’ or foundational and general theory, which by its essence is absolute and not contingent.

      • Hmm. I think that’ true of some ecologists. The school of ecology that Mick Crawley called the WIWACS (“world is infinitely wonderful and complex school” of ecology). But I’ve no idea how common the WIWACS are and I doubt they’re a majority. But I guess we just have very different anecdotal impressions of ecologists’ motivations for getting into ecology?

        FWIW, years ago at Tony Ives’ MacArthur award lecture at the ESA meeting, about 2/3 of the audience by a show of hands denied that ecology was about “general laws”.

  7. What about the mathematics in these kinds of papers?
    Or this more recent paper
    And then there is John W. Terborgh’s nice little review of the shift between the old bottom up models and the newer top-down modelling -it is a couple of years old, but still interesting, since it suggests an alternative to models assuming that carrying capacity and niche specialization determined diversity, whereas the trophic top down modern suggested it w the presence of keystone species that had more impact…
    And then there is this stuff:
    “…All of the animal species on earth are consumers, and they depend upon producer organisms for their food. For all practical purposes, it is the products of terrestrial plant productivity that sustain humans. What fraction of the terrestrial NPP do humans use, or, “appropriate”? It turns out to be a surprisingly large fraction. Let’s use our knowledge of ecological energetics to examine this very important issue. (Why NPP? Because only the energy “left over” from plant metabolic needs is available to nourish the consumers and decomposers on Earth.)
    We can start by looking at the Inputs and Outputs:
    Inputs: NPP, calculated as annual harvest. In a cropland NPP and annual harvest occur in the same year. In forests, annual harvest can exceed annual NPP (for example, when a forest is cut down the harvest is of many years of growth), but we can still compute annual averages.
    Outputs: 3 Scenarios
    How much NPP humans use directly, as food, fuel, fiber, timber. This gives a low estimate of human appropriation of NPP.
    Total productivity of lands devoted entirely to human activities. This includes total cropland NPP, and also energy consumed in setting fires to clear land. This gives a middle estimate.
    A high estimate is obtained by including lost productive capacity resulting from converting open land to cities, forests to pastures, and due to desertification and other overuse of land. This is an estimate of the total human impact on terrestrial productivity.
    Units: We will use the Pg or Pedagram of organic matter (= 1015 g, = 109 metric tons, = 1 “gigaton”) (1 metric ton = 1,000 kg).
    Table 1 provides estimates of total NPP of the world. There is some possibility that below-ground NPP is under-estimated, and likewise marine NPP may be underestimated because the contribution of the smallest plankton cells is not well known. Total = 224.5 ngp…”

  8. Here are some quotes that might be relevant to this discussion.

    Masatoshi Nei (2013, ‘Mutation-Driven Evolution’): “During the twentieth century, an impressive amount of mathematical theories has been developed, but as large portion of them, including some of mine, have remained unused because they are not realistic. In the future it would be important to develop theories that are based on solid biological principles. It should also be noted that we do not necessarily need mathematical models for understanding the evolution of complex morphological characters. In this case molecular study alone is often sufficient, as will be discussed in the following chapters.”

    Lynn Margulis (2011, “Population geneticist Richard Lewontin gave a talk here at UMass Amherst about six years ago, and he mathematized all of it—changes in the population, random mutation, sexual selection, cost and benefit. At the end of the talk he said, “You know, we’ve tried to test these ideas in the field and the lab, and there are really no measurements that match the quantities I’ve told you about.” This just appalled me. So I said, “Richard Lewontin, you are a great lecturer to have the courage to say it’s gotten you nowhere. But then why do you continue to do this work?” And he looked around and said, “It’s the only thing I know how to do, and if I don’t do it I won’t get my grant money.”

    Jerry Coyne (2011, “I called up Dick [Lewontin] this morning and read him Margulis’s quote. He said that it completely mischaracterized his views and what he must have said at Amherst. Lewontin said that he thinks that purely mathematical models of population genetics have largely failed to help us understand the distribution of gene frequencies in nature, because those models often make assumptions that are either incorrect or untestable. So while mathematical theory in population genetics has had some successes, he said, it hasn’t been nearly as useful as we hoped.”

    • Yes, I now recall seeing another published remark of Lewontin’s along the lines of the one that Coyne reports. This is indeed the sort of thing ones sees a fair bit of in ecology. Thanks for passing those quotes along.

      Margulis is unusual and something of an iconoclast. I spoke to her as a grad student when she visited Rutgers. She said (among other…unconventional things) that John Maynard Smith was a great natural historian, but it was a shame he didn’t use his natural historical knowledge. Which in my view was a pretty serious misunderstanding of what John Maynard Smith was up to in his work.

  9. Somehow I missed this yesterday so I’m late to the party. “Evolutionary Biology” is a big tent and from where I sit, I see lots of sub-areas of evolutionary biology that are devoid of models or model thinking. It’s filled with fuzzy, qualitative thinking resulting in plausible stories. Citations of theoretical work by empiricists are largely cursory — that is they aren’t testing the models. The areas I’m thinking of are multivariate phenotypic evolution (Lande-Wagner-Turelli type models), phenotypic plasticity (which is desperately seeking models although Lande has moved in here), and performance trade-offs (in the sense of Arnold’s morphology-performance-fitness).

Leave a Comment

Fill in your details below or click an icon to log in: Logo

You are commenting using your account. Log Out /  Change )

Google photo

You are commenting using your Google account. Log Out /  Change )

Twitter picture

You are commenting using your Twitter account. Log Out /  Change )

Facebook photo

You are commenting using your Facebook account. Log Out /  Change )

Connecting to %s

This site uses Akismet to reduce spam. Learn how your comment data is processed.