Yes, the IDH is a zombie: response to Karl Cottenie

Karl Cottenie has a thoughtful post up responding to my post on the zombie idea of the intermediate disturbance hypothesis. That’s what I was hoping to do: get people to stop and think, so I’m really glad Karl did so. I thought I respond here, both because my response is a little long, and because I think Karl’s probably given voice to what many readers of my original post thought. So go read what he has to say, then come back here (because otherwise what I say below won’t make much sense to you…)

…Welcome back! Okay, I’ll take Karl’s comments on each of the three zombies in turn:

1a. This first zombie isn’t really about trade-offs (UPDATE: I mean, yes, there’s a trade-off in there, but that’s not the zombie part of the idea). The zombie bit is the idea that, if density is reduced low enough by some density-independent factor, competitive exclusion can’t happen. I’m glad that Karl agrees that that’s just wrong.

1b. Yes, there are trade-offs between competitive ability and other things which really do allow stable coexistence. That’s what models like the ‘successional niches’ model of Pacala & Rees are about. I would only add that you have to be precise about what those other things are. In particular, whether or not “stress tolerance” or “disturbance tolerance” can trade off with competitive ability to produce stable coexistence is sensitive to precisely what you mean by “stress tolerance” or “disturbance tolerance”. Imprecision about this in verbal arguments is one unfortunate source of zombie strength.

1c. It’s a bad idea to think of transient dynamics like those in Violle et al. as support for a mechanism that’s supposed to work at equilibrium, or on average over the long run. If you’ve ever played around with simulating even quite simple ecological models, you know that transient dynamics can be very complex, and need have no relationship to long-term outcomes (see, e.g., Alan Hastings‘ work). It’s trivially easy to produce a model that lacks any coexistence mechanisms whatsoever (zombie mechanisms as well as real ones) and get it to produce any transient peak in diversity you might want.

I’m not the only one to write about how easy it is to misinterpret transient dynamics. I think Elizabeth Borer did a paper on this in Ecology a few years ago in the context of people mistakenly using short term transient data to test long-term predictions about host-parasitoid dynamics and apparent competition.

2. Karl’s disagreement with me here may be a matter of po-tay-to, po-tah-to. But I’m still inclined to defend my pronunciation, if that makes any sense. 😉 The zombie idea here is the idea that “interruptions” are key. That’s wrong. If you think that’s correct, then you would expect my suggested “control” experiment (impose increased but continuous density-independent mortality on all species) to have no effect on the rate of exclusion. But in fact, increased continuous mortality slows the approach to equilibrium just as much as periodic mortality events do, which shows that “interruptions” are irrelevant in Huston’s model.

And I do think that matters. After all, the whole reason people care about disturbances is that disturbances create (or are thought to create) effects that would not occur in an undisturbed, steady-state world. Except that in Huston’s (1979) model, disturbances do no such thing.

I really don’t think this has to do with disturbances having various different aspects (duration, extent, severity, frequency…), which of course they do. And I don’t think it’s about “eliminating temporal dynamics” (not sure what Karl means when he says I’m trying to do this). This is about misinterpreting why a model behaves the way it does. Yes, there are fluctuations in the population dynamics in Huston’s model–but they have no causal effect on the outcome of competition. They’re an epiphenomenon. And that misinterpretation isn’t innocuous, or a technicality–it leads one to make real mistakes (like mistaken prediction of the outcome of an experiment manipulating continuous, density-independent mortality rate).

3. Here again, Karl seems to think that temporal sequences of events–say, the fact that populations sometimes go up, and then go down–have some effect or reveal some mechanism, when in fact they don’t. Again, if you think that fluctuations are what matters in Hutchinson (1961), then you would predict that coexistence could be maintained in a system in which the environment fluctuates at intermediate frequency, but favors one species over the others on average. And you’d be wrong.

In general, it’s really tempting to inspect time series data and try to figure out the processes that generated the data. Especially in time series where the most visually-obvious feature is big fluctuations in abundance. And inspecting time series is a perfectly good starting point for thinking about the processes that might’ve generated them–but it’s usually a bad idea to trust the hypotheses you come up with without checking them mathematically. For instance, the state of a flipped coin fluctuates over time–one time it comes up heads, the next time it comes up tails, then it might come up tails again, etc. But you can’t just inspect a time series of coin flips and glean any meaningful information from it (in particular, whether the coin is fair on average, in the long run). People who think they can lose a lot of money gambling (“The coin’s come up heads several times in a row, it’s must be due to come up tails now, so I’ll bet on tails!” Compare: “Species 1 went up while species 2 went down, and later the reverse happened, that must be why they coexist, I’ll bet on them continuing to do so!”)

Like I said in the original post, there absolutely are systems in which disturbances matter in the long run. Those are nonlinear and nonadditive systems–see Peter Chesson’s work for discussion. And some nonlinear, nonadditive models even predict peaks in diversity at intermediate disturbance (though they often don’t predict that pattern–see Miller et al.). But none of that validates these zombie ideas. If an invalid and a valid argument both lead to the same conclusions, the valid argument doesn’t validate, or in any other way support, the invalid one. “Socrates is a man, and all men are mortal, therefore Socrates likes ice cream” is an invalid argument, and it’s still invalid even though “Socrates is a man, and all men like ice cream, therefore Socrates likes ice cream” is a valid argument. Zombie arguments about the IDH don’t get any “reflected glory” from non-zombie ones.

Nor do invalid zombie ideas about the disturbance gain any support from empirical data. If you think they do, you’re misinterpreting the data. The situation here is very much in contrast to the usual situation with theoretical models. All theoretical models are false in some way. Usually, that’s because they make some simplifying assumptions that aren’t exactly true, and may even be quite false. When we go and test their predictions empirically, basically what we’re asking is whether the assumptions are close enough to being true to make correct predictions. But in the case of zombie ideas about the IDH, the falsehood isn’t in (or isn’t just in) the assumptions, it’s in the logic with which the predictions are derived from the assumptions. The assumptions don’t logically imply the predictions, and so evidence for the predictions doesn’t provide any evidence for or against the assumptions.

Again, I’m not trying to pick on Karl here–the questions he raises are good ones. I think the above answers are good, and I hope he and other folks will thinks so too.

11 thoughts on “Yes, the IDH is a zombie: response to Karl Cottenie

  1. Really interesting discussion on this topic – it definitely making me think hard to try and keep up! I thought I’d try to summarize what I’ve understood of it so far and maybe you can help clarify my understanding 😉

    IDH basically argues that too much disturbance leaves only very stress-tolerant species, too little disturbance results in faster competitive exclusion and intermediate disturbance (“intermediate” in frequency or severity or some other aspect of disturbance) slows competitive exclusion by increasing overall mortality and creating a variety of temporal niches in which different species have the highest growth rate, thus allowing multiple species to temporarily co-exist.

    It seems to me that Jeremy’s objection is that these dynamics do not, and cannot, prevent long-term competitive exclusion. Even in a fluctuating, disturbed environment, eventually one species will exclude the other(s), given that the system reaches equilibrium – and whether the disturbance is severe but episodic or less severe and continuous doesn’t change that. He also argues that disturbance does not minimize or eliminate competition, it just changes the competitive balance (ie which species is the better competitor changes as conditions change) – and on this I think he and Karl agree.

    Karl’s argument is based on an understanding of systems that are not at equilibrium. Disturbance can (but doesn’t always) promote co-existence on short (but I would argue ecologically-relevant) time scales – and these are often the time scales that ecologists measure and observe (whereas equilibrium dynamics are best predicted using a modeling approach or mesocosm experiments).

    In other words, I don’t think Karl and Jeremy really disagree, I think they are addressing different issues. Jeremy, looking at long-term dynamics, says IDH can’t explain long-term coexistence in a system moving toward equilibrium. Karl, looking at short-term dynamics in a non-equilibrium system argues that IDH can explain co-existence on that scale. Of course, even in the short-term IDH only would explain co-existence in some systems, where other systems would be influenced by other factors (dispersal limitation, for example).

    Thanks for the interesting discussion, all! I look forward to your thoughts or comments on the synthesis above 🙂

    ~Jennifer

  2. Hi Jennifer,

    Thanks for your comments, glad you’re enjoying the posts.

    I can’t speak for Karl and so can’t say if he’s really worried exclusively, or mainly, about short-term, transient dynamics as opposed to my concern with long-term outcomes.

    But for those readers who are interested in short-term or transient dynamics, perhaps because “that’s all we can measure”, or because “those are still ecologically-relevant timescales”, I have a few remarks (not directed at you necessarily, or at Karl, but rather at some hypothetical ecologist):

    1. If what you care about is short-term transients, why the heck would you ever use models that are about, or claim to be about, long-term outcomes to guide your work? Because seriously: pretty much every well-known and widely-studied model on every topic in ecology, including both zombie and non-zombie ideas about disturbance, is about, or claims to be about, long-term outcomes, not transients. And if you think (or hope!) that transients will generally look sort of like the long-term outcome, I’m sorry, but they often won’t. See, e.g., Alan Hastings’ and Elizabeth Borer’s work, cited in the post, Neubert & Caswell’s work on ‘reactivity’ (even stable systems can temporarily move FURTHER from equilibrium after being perturbed before eventually returning), my 2007 Oikos empirical paper on the transient dynamics of trophic cascades, Jim Brown’s classic 1984 work on the contrasting transient and long-term effects of competing seed predators on one another, and many, many other papers. Unfortunately, it’s probably impossible to offer up any rules of thumb on when transient dynamics will resemble long-term outcomes and when they won’t.

    2. If you would really like to study long-term outcomes, but transient dynamics are all you can measure in your system, why don’t you change study systems? Alternatively, why don’t you stick to asking questions you can actually answer with short-term data? Or, why don’t you find a *rigorous* way to infer something about long-term outcomes from short-term data? (Note that “Collect short-term data, compare to theoretically-predicted long-term outcome” is NOT a rigorous thing to do). For instance, if you’re interested in long-term coexistence, you can do short-term mutual invasibility experiments (i.e. experiments that just test whether rare competitors tend to “bounce back”, which is a short-term question), use them to parameterize dynamical models of your system, and then use the models to project the long-term outcome expected from your short-term data. Folks like Jon Levine have been doing exactly that. That approach isn’t foolproof (e.g., if you’re parameterizing a bad model, the long-term projections will be wrong). But no approach is foolproof, and the potential drawbacks of that particular approach are knowable and checkable in various ways (e.g., you can compare the projected long-term outcome of competition to observed species abundances, or long-term time series data, as in the work of Jon’s former postdoc Peter Adler). So I’m sorry, but if you say “I’d like to study long-term outcomes, but transients are all I can measure, and long-term models are all I’ve got to interpret those measurements”, you are worrying about a totally self-imposed problem.

    3. Talking about “short-term but ecologically-relevant timescales” is sometimes something we have good reason to talk about (e.g., “these competitors have coexisted for 100 generations, which is not forever but is long enough to demand an explanation”). And it’s sometimes something we have to talk about (e.g., “the law obliges management decisions to be made on this timescale”). But in my experience, it’s often shorthand for “I don’t have long-term data, but I want to publish the data I do have, so I’ll call them data about ‘ecologically-relevant timescales’.”

  3. Thanks for your response! It gives me plenty to think about and it’s a great reminder about how important it is to be careful about how we draw conclusions given the limitations of our dataset.

    I think one of the greatest challenges in ecology is inferring long-term dynamics given our limitations as short-lived observers – I appreciated your comments about how that can be done. I also find it really interesting how short and long-term dynamics come together in often completely unpredictable ways. I guess there’s plenty of room in ecology to study both, as long as we’re explicit about the kind of data we have and the limitations thereof!

    ~ Jennifer

  4. Pingback: Non-zombie ideas in ecology: how disturbance and environmental fluctuations ACTUALLY affect coexistence (part 1) | Dynamic Ecology

  5. Is your zombie a straw man of the historical version of IDH? Do modern proponents think of IDH as being about anything but trade offs? And if they don’t is this an issue? People used to think of calculus needing Infinitesimals, which was shown to be logically silly, but instead of dismissing calculus people just fixed the underlying logic (Cauchy’s delta/epsilon formulation). I feel Karl has made a clear argument that we don’t think about IDH anymore in the manner you suggest. All you seem to show is that people used to think about it that way and smart theoreticians have shown us how to use the concept clearly. Seems like an odd zombie if it is the case.

    • Hi Gabriel,

      You ask a reasonable question, but no, the truth is that plenty of modern proponents of the IDH do hold precisely the zombie ideas I criticize. And for whatever it’s worth, I’m not the only one who thinks so. I have an ms in press at TREE, closely based on these posts, arguing that the IDH should be abandoned. Four reviewers all liked the ms and found the argument to be well worth publishing, which I don’t think they would have if they thought I was just attacking old-fashioned ideas that nobody believes in any more.

      Here’s a more objective line of evidence: Connell (1978) has been cited over 1000 times in the last 5 years alone, and its annual citation counts is increasing exponentially, at the same rate as the exponential increase in the number of ecology papers. Annual citations of Huston (1979) also are higher than they ever have been and continue to increase, albeit at a somewhat slower rate than for Connell (1978). Meanwhile, modern papers refuting those zombie ideas–Chesson and Huntly 1997, Roxburgh et al. 2004, Shea et al. 2004, Miller et al. 2011, others–are cited much less often, and their annual citations bounce around rather than increasing exponentially. That doesn’t look to me like what should be happening if everyone has stopped believing in these zombie ideas.

      Here’s another objective line of evidence: as I’ve noted in other posts, even recent textbooks, like the current edition of Ricklefs and Miller, repeat these zombie ideas.

      Now, to be fair, modern IDH proponents also believe in some non-zombie ideas, particularly competition-colonization trade-offs and other trade-offs. But that isn’t very helpful in terms of rooting out zombie ideas, since many people fail to distinguish between non-zombie and zombie ideas about the IDH. As Shea et al. 2004 notes, IDH proponents in general have been very poor at distinguishing quite different theoretical claims (and indeed, even distinguishing empirical and theoretical claims!)

      Sorry, I sincerely wish you were right, but you’re not. The zombie ideas about the IDH that I attack are just as widespread as they ever were. And frankly, I doubt that you’ll see much signal of my attacks (or my forthcoming TREE article) in citation patterns in coming years. Ideas that are so widely presented in textbooks, and still adhered to and pursued by so many prominent researchers (Phil Grime and his many former students, for instance), can only be rooted out very, very slowly. The timescale, I think, is basically set by the rate at which people who believe in these ideas retire and are replaced by people who don’t believe in them (or at least don’t care about them enough to teach or research them). There are historical cases in science of lots of people changing their minds en masse about some previously well-established claim, but they’re pretty rare. That Darwin managed to change a fair number of minds about evolution vs. special creation is a massive credit to his powers of persuasion (and to the skill and organization with which his friends developed and cultivated professional influence).

      • Thanks for the thorough reply!

        Your citation evidence I don’t find convincing, as citations of Connell could be nothing more than an offhand way of saying you are using IDH, not that the people care about the exact reasoning in the paper. Again I think this is analogous to Calculus where most people would think of Newton and Leibniz and not even know who Cauchy was, even though the modern theory all comes from the latter. This seems exactly the same with regards to Chesson and Huntly. They give a technical paper, like Cauchy’s delta/episilon proofs, that require much more subtle understanding, so I see no reason why general researchers would cite Connell like non mathematicians think of Newton/Leibniz and specialist will cite Chesson and Huntly (ie Cauchy). This is not proof that the former believe in the zombie ideas you put forward.

        Also in regards to your pessimist vision of how ideas change in a field, again, I feel you miss the possibility that new researchers will simply co-opt the term IDH to mean the correct concept. So if in 10 years young researchers (lets say students of Karl Cottenie) are still describing IDH mechanisms (but using trade-offs etc), it simply might be that they no longer carry the confused baggage you describe. If this is the case has the Zombie been put down?

      • Sorry, unable to share your idealistic vision of a world in which zombies may appear to be present but are in fact absent. If lots of people are citing Connell, or Huston, but not citing Chesson and Huntly, that means they haven’t absorbed Chesson and Huntly’s critiques of Connell and Huston. Not to crush your spirits or anything, but that’s the way it is. 😉 Have a look at Shea et al. 2004, the poll I did on belief in zombie ideas about the IDH (many, many respondents indicated that they believed in it before reading my posts), our current textbooks, the fact that TREE is publishing my paper on this (again, why would they do that if I was attacking an idea nobody believes in anymore, like phlogiston or a flat earth?)…If an analogy with the history of calculus suggests otherwise to you, sorry, but that just means it’s not a good analogy. It’s great that you’ve absorbed the right way to think about things-but sadly, you’re still in a minority.

        If you still don’t buy it, I encourage you to look up the many recent papers that cite Connell and Huston, but don’t cite Chesson and Huntly. Have a look at what those authors mean by “IDH”. I doubt you’ll find any cases where authors clearly mean “the non-zombie ideas developed by Peter Chesson, even though we don’t actually cite him”.

        Yes, it’s possible the meaning of the term “IDH” will shift. That’s a possible symptom of the changing views of the field as a whole. But I don’t see what that has to do with the *rate* at which the views of the field as whole change (however those changed views are manifested).

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