The previous post referred to a philosophy talk about Robert MacArthur, his observations of feeding warblers, and the competition models which his warbler work helped inspire.The speaker apparently drew some general lessons about the conduct of ecological science from MacArthur’s example.
Maybe I’m just grouchy today, but I have to ask: is it really healthy for ecology, and for those philosophers and historians who study ecology, to place so much weight on so few historical examples? Does the example of Robert MacArthur and his warblers really have anything left to teach us about ecology or how to do it? I mean, I know he was and remains hugely influential, and rightly so. But should he, or any ecologist, really be treated like Shakespeare or the Bible, an inexhaustible source of inspiration and insight? MacArthur has been dead for forty years, and it’s only in the broadest and loosest sense that any ecologist these days actually does “MacArthurian” ecology, however you might define that. Seriously, do you think any journal today would even publish MacArthur’s warbler data? Much less take those data as strong evidence for his competition model? And it’s not just that our standards of evidence are higher today, it’s more profound than that. Ecology today, even as practiced by those who are self-consciously influenced by MacArthur and take him as a role model, is not just “MacArthur, only with better data.” And by that I don’t just mean that today we worry about forces other than competition. For instance, West et al. (1997), hugely influential and co-authored by two ecologists who hold MacArthur in the highest regard, strikes me as very far from the sort of thing Robert MacArthur himself would ever have done. Unless you regard as “MacArthurian” any paper concerned with explaining general patterns, which I really don’t think you should.
In continuing to pay so much attention to MacArthur, we necessarily ignore other voices from ecology’s rich past, we misunderstand our present (including the influence of MacArthur on the present) by viewing it through an outdated lens, and (as Peter Kareiva has argued) we misdirect our future efforts. MacArthur was an important ecologist and in many ways remains a fine role model. But he’s far from the only important ecologist, and far from the only role model. Just for starters, I’d suggest that modern students of ecology can learn at least as much from Gause as they can from MacArthur.
I should emphasize that, not actually having seen the talk Joan saw, I have no idea why MacArthur was chosen as an example and I’m totally not criticizing the talk or the speaker. The subject of the talk just happened to prompt the above thoughts, which otherwise probably would’ve been prompted by something else at some point.
UPDATE: Can’t believe I forgot to mention this in the original post, but I count myself among those who had to get over MacArthur. In grad school, I did a side project on the propagation of indirect effects in food webs, which I ended up publishing in Oikos (Fox and Olsen 2000). This genesis for this project was that I’d read a famous but quite odd paper of MacArthur’s on complexity and stability (MacArthur 1955). I decided that figuring out what the heck MacArthur was talking about and then testing it would make for a good side project. In the end, I think my paper was perfectly fine. But the starting point (“I’m going to identify an interesting question by doing textual exegesis on an old paper of Robert MacArthur’s”) was not one I would ever choose again.
UPDATE #2: Jay Odenbaugh, the philosopher who gave the talk referred to in the previous post, actually has done a lot of interesting-looking work in philosophy of science, as applied in the context of ecology (a field of science that philosophers until recently have not given much attention). As someone who’s always encouraging other ecologists to read more philosophy, I’m embarrassed that I wasn’t already familiar with all of his work (update: especially since I learned that he got his PhD at Calgary, where two of my closest colleagues were on his committee!) I’m looking forward to rectifying that. Interestingly, he is working on a paper on philosophical issues raised by Hubbell’s neutral theory. So Jay is not someone whose attention is drawn only to a limited range of famous historical figures in ecology.
UPDATE #3: Jay Odenbaugh himself has popped up in the comments with some very thoughtful remarks. Thanks for stopping by Jay!
Dynamic Ecology 
The talk was by a philosopher, and MacArthur was one of his main subjects. Jay Odenbaugh has done some really interesting work. I guess the philosophers mainly study the big guns, partly because they are also interested in their impact on us. If I were a starting out ecologist, I’d look hardest at people studying microbial systems.
Thanks for the context Joan. I can certainly see why philosophers and intellectual historians would want to focus on the “big guns”. It’s not that I think they shouldn’t. It’s just that I also wonder what that approach misses, and why certain big guns, such as MacArthur, seem to attract such a disproportionate share of the attention. For instance, population ecologist Dennis Chitty, although well-known, was never a “big gun”. But his account of his research, Why Do Lemmings Commit Suicide? would be very interesting fodder for philosophers and intellectual historians interested in ecology. Chitty is very explicit about his (arguably problematic) philosophy of science, and about the ultimate failure of his entire research program. He was also part of a very influential research group.
Right now I’m reading Cooper’s The Science of the Struggle for Existence, which is a philosopher’s take on key debates in the history of ecology. I plan to post a review once I’ve finished it (which will be a while since I only have time to read it on the bus to and from work). So far it’s quite good, even if I would quibble with some bits.
“If I were a starting out ecologist, I’d look hardest at people studying microbial systems.”
Then you’d want to look hard at Gause! 😉
One interesting thing Jay Odenbaugh is doing in that work is trying to figure out what MacArthur’s theory contributed to integrating ecology with genetics. In the background is philosopher Philip Kitcher’s idea that theories explain things by unifying them — making things that seemed to have nothing to do with one another (like tides and falling objects) understandable as implications of one theory (like gravitation).
But you’re right: ecology, history, and philosophy are impoverished when we focus on too few examples. Science students would be at a loss if textbooks didn’t set out classical examples, but rehashing those examples can produce what you’ve called zombie ideas, especially when they are repeated without sufficient attention to the original research.
Yet, undermining those zombie ideas is a good reason philosophers and historians have spent time on the tired examples! I recently tried to do this with one of the oldest, tiredest textbook zombies, Clements and Gleason, to argue that we’ve made them into inaccurate caricatures: Eliot, C (2011). “The legend of order and chaos: Communities and early community ecology” in deLaplante, et al, eds, Philosophy of Ecology, pages 49–108, Elsevier. And historian Joel Hagen made some headway on Clements earlier: Hagen, J. B. (1988) “Organism and environment: Frederic Clements’s vision of a unified physiological ecology” in Rainger, R, et al, editors, The American Development of Biology, Rutgers.
Thanks for the very interesting comments.
Re: Kitcher, he’s on my list of philosophers I need to read more of. I’m currently teaching a graduate seminar on Darwin’s Origin of Species, in which students read and discuss the first edition and some related readings. I want to devote one session to the notion of unification as a virtue of scientific theories, and perhaps even a mark of truth. The Origin is of course a famous example of unification. But conspiracy theories also unify and “explain” apparently-unrelated facts–which is often taken as evidence against them. And there are scientific conclusions in which we’re highly confident precisely because we have several independent grounds for believing those conclusions. If those grounds were “unified”, they’d no longer be independent. Can you suggest a useful article or two here to give non-philosophy students the “lay of the land”? Maybe something from the Stanford Encyclopedia of Philosophy?
Historical caricatures absolutely are a key source of old, tired zombie ideas, and yes, the whole Clements vs. Gleason opposition that appears in every undergraduate ecology textbook is one of the oldest and tiredest. It physically pains me when contemporary ecologists (none of whom have ever actually read Clements or Gleason) trot out these opposing caricatures in the Introduction section of their papers as a way of motivating their research. It’s bad enough that anyone today would motivate their research by reference to long-dead ecologists, but it’s even worse that anyone would motivate their research by reference to caricatures of long-dead ecologists.
Mousetrap is an interesting blog that looks to undermine historical caricatures in ecology and evolution by going back to the original sources. Have you seen it?
Sure, on unification: Kitcher’s most accessible presentation of his unification ideal, which addresses your questions and is good for non-phil students, is in “Believing where we cannot prove,” Chapter 2 of Abusing Science, see especially p. 45ff.
However, there’s also a nice account of some of the difficulties with explanation-as-unification in Jim Woodward’s SEP article on Scientific Explanation. And specifically on unification in Origin, and reasons not to think that’s Darwin is just unifying, see Waters, C. K. (2003) “The arguments in the Origin of Species” in Hodge, M. J. S. and Radick, G., editors, The Cambridge companion to Darwin (also quite accessible).
Thanks very much for the references, Chris. The Darwin literature, and the philosophical literatures on explanation and unification, are all vast. I was a bit afraid that digging up appropriate material would be like looking for a needle in a haystack.
Good post. I had an instructor in grad school who gushed over G. Evelyn Hutchinson, like he was a God. Maybe it was because he died around that time but it was strange nonetheless. It’s a fine line between appreciation of the approaches and findings of others in times past, and hero worship.
But are we still having these discussions about theory development in ecology? Is this stuff never going to die? I’m all for understanding the big picture as much as anyone, but not at the expense of the transient and site-specific dynamics that are essential to effective ecosystem management, and which also build the database upon which truly comprehensive models can be built or improved upon.
Count me as one who greatly values the natural history and other contributions of those in times past, and in fact believes that they are greatly undervalued in many cases–and I’m talking about going back to von Humboldt and Linnaeus and before. The irony of this thing is that those who imagine the “glory days” of MacArthur etc only want to go back just that far–when you could construct a nice theory and get a name for yourself based on some limited set of observational data. Theories which are generally completely useless for any sort of management level application I might add. I think you could even argue that the MacArthur/Hutchinson era represents a *low* point in ecological undersatnding–the naturalists of the 19th century having a very holistic perspective derived from their vast observational experience, and today’s ecologists having access to much more powerful tools (and data sets).
The piece by Kareiya is says it all I guess.
Re: Hutchinson, I do wish people would stop citing his paradox of the plankton paper (Hutchinson 1961), and not just because Hutchinson’s own proposed solution to the paradox is a zombie idea (and I say that as someone who’s cited it myself!) It’s not as if Hutchinson (1961) was the first or only paper to recognize that coexisting competitors demand an explanation. And if you read that paper (which I actually have done), it’s not like it’s this bottomlessly rich and profound thing, shot through with all kinds of insights. It’s not the Origin of Species (which is a rich classic that actually does reward repeated reading).
Hutchinson’s idea about niches as “n-dimensional hypervolumes” is, along with other old ideas about “niches”, another set of zombie ideas we ought to quit citing. The best modern thinking about how species coexist does not fit at all comfortably into Hutchinson’s verbal framework; Leibold (1995 Ecology) points this out. A lot of contemporary misunderstandings about how coexistence works come from people either ignoring contemporary thinking in favor of Hutchinsonian hypervolumes, or misunderstanding contemporary thinking because they (mis)read it through the lens of Hutchinson.
I should really do a post on this. List all the “classic” papers in ecology that we should quit citing because they have nothing left to teach us. The well is dry, so we should stop returning to it (or worse, we now know the well is poisoned and will turn you into a zombie if you drink from it). Hairston, Smith, and Slobodkin (1960) is one–not a zombie really, just totally played out.
Could then follow it up with a post on “neglected should-be classics”–old forgotten papers that are very relevant today and are worth revisiting. I’ve already suggested Gause here, and not the abridged “textbook caricature” who merely discovered the competitive exclusion principle. I’m talking about the unknown guy who had a thoroughly modern understanding of what we can learn from model systems, and how to link theoretical models and data, and who (in contrast to someone like MacArthur) really did just lack the technical tools to fully implement his approach. A lot of the best modern population and community ecology really is “Gause, but with better data and better stats”.
Part of the reason certain papers attain iconic status is because of copycat citation–everybody cites them because everybody else cites them. Here’s a good rule of thumb: if you feel the urge to cite something only because everybody else has–fight it! Or to put it another way, the Introduction of your paper should talk about ecology, not about what ecologists (even famous dead ones) have said about ecology. What people say about ecology changes all the time, and is often wrong. If you’re studying interesting or important ecology, you should be able to explain why it’s interesting or important without relying on the authority of famous dead people (or anyone else). Just because someone, or even lots of someones, says something is interesting or important or true doesn’t make it interesting or important or true.
Note that I still think students should read these old papers–you need to know the history of your field. But one of the best reasons to study history is so that you’re not condemned to repeat it!
Great ideas for posts. I would be especially interested in the “neglected, would be classics” papers. That would be a definite service to everyone IMO–and would hopefully generate a lot of suggestions and conversation as well.
Re: update #2, I had noticed the same thing. He is also apparently working on an evaluation of climate model structures and predictions and what they mean for “unification”.
Yes, climate models are a good contemporary example of purported “robustness”–independent models, making different assumptions, leading to the same conclusion, thereby giving us confidence that the conclusion is true even if no single model is true (cf Richard Levins’ line about how “the truth is the intersection of independent lies”). Of course, that argument breaks down if the models share some assumptions (perhaps hidden, implicit ones) and so aren’t truly independent. I’m sure all climate models share some assumptions, so I’ll be interested to read Jay’s work on this.
Back in the early ’80’s the philosopher Bill Wimsatt argued that “independent” evolutionary models purporting to demonstrate the implausibility of group selection all shared key implicit assumptions that drove the results, and that in fact group selection was not implausible at all.
Even when you have truly independent arguments, the conclusions aren’t necessarily true, of course. Kelvin’s calculation of the age of the earth based on its rate of cooling from an initially-hot state basically lined up with the calculations of von Helmholtz and Newcomb based on the time it would take the sun to condense down to its current size. Both also roughly lined up with the later calculations of Darwin’s son George, based on the time it would take tidal friction to slow the earth’s rotation to its current 24 hour period. The calculations were truly independent, but each was thrown off by a then-unknown, and thus omitted, factor (radioactivity in Kelvin’s case, nuclear fusion in the case of von Helmholtz and Newcomb). So the fact the three calculations all gave roughly the same answer was just an unfortunate coincidence. See http://en.wikipedia.org/wiki/Age_of_the_Earth#Early_calculations.
The argument for the likely robustness of independently-derived conclusions also has been criticized on other grounds. Philosopher Steve Orzak has a paper critiquing Richard Levins’ ideas on this.
He will have his work cut out for him because these are among the most complex pieces of science known to man, and there are more than 20 of them now, so I too will be interested in what he says.
Climate models are definitely not truly independent. In fact there’s a distinct and traceable phylogeny (see http://www.aip.org/history/climate/xAGCMtree.htm) that stems from their origin in certain weather forecasting groups during the cold war (UCLA, Princeton, etc). They all share for example, a fundamental dependence on the Navier-Stokes equations that describe fluxes of atmospheric mass, energy and momentum between grid cells, as well as similar radiation transfer codes. But they differ in a number of other important things, such as sub-grid cell parameterizations (e.g. for clouds), convection models and who knows what all. There is a formally established model intercomparison project called PCMDI that is all over this (http://www-pcmdi.llnl.gov/new_users.php) As far as I am aware this is the most systematized and intensive model evaluation project in all of science, and certainly in the earth and environmental sciences.
I think this is a really great blog having been reading it for a little while – and thanks for mentioning my work.
With regard to a couple of questions here are some thoughts. For any episode in the history of science there are many, many influences. To single out a few figures is always to risk sampling bias (and it is hard to get those figures right – they are subject to philosophical misinterpretations – Chris has corrected my own work on that score). However, some figures are extremely important in the history of the discipline and its self-conception and Robert H. MacArthur is that with respect to community ecology.
Having said that, as a philosopher and part-time historian, I think it is crucial to ask why was he important and not simply assume that he was. Equally importantly, I think we cannot assume that his importance lies in what he did right but also in what he did wrong. It my estimation, we cannot understand how science progresses when looking at what is happening right now. We need some critical distance to appreciate and to critique the work that is being done.
So, why is MacArthur important? I think he offered an approach to ecology that was very appealing. First, you offer simple, analytic models to explain “blurry” patterns. Second, you evaluate those models with qualitative comparisons between the model predictions and the said patterns. Third, you postulate that community patterns are in the main the result of interspecific competition and that history is inessential to ecological outcomes. Finally, you disregard conceptual debates over what “communities” are, etc. In some cases, MacArthur and his colleagues articulated really powerful theories that have inspired serious fieldwork and other models (i.e., island biogeography). On the other hand, they offered some dead – like really dead – ends (i.e., limiting similarity models).
Suppose that MacArthur and his colleagues were mostly wrong. Still, I think the discipline owes them quite a debt. In the offing we find metapopulation models, macroecology, the recognition that history wasn’t “eclipsed”, a focus on null hypotheses and model selection more specifically, the realization that competition is one amongst many mechanisms, and so on.
MacArthur spelled out a good ol’ Kuhnian paradigm and tried to take it places. No doubt things didn’t go as planned but such is the way of science.
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