Phylogenetic community ecology is one of the biggest bandwagons in ecology right now (and before you get upset with me for saying that, click the link to find out what I mean by “bandwagon”). Much of this interest was sparked by Webb et al. (2002), who suggested that, by mapping co-occurring species onto a phylogeny of the species pool (the set of species thought to potentially be able to occupy the study site), “a simple logical framework can then be employed to infer mechanisms of contemporary coexistence” (Webb et al. 2002, p. 478). Specifically, they suggested that co-occurrence of phenotypically-similar species indicates “habitat filtering”, meaning roughly that community membership reflects species’ abilities to tolerate the local abiotic environment. Conversely, co-occurrence of phenotypically-different species means that similar species are being competitively excluded (=limiting similarity). If, as is often the case, phenotypic traits are phylogenetically conserved, so that closely-related species tend to be phenotypically similar, co-occurrence of closely-related species (“phylogenetic clustering” or “attraction”) implies habitat filtering, while co-occurrence of distantly-related species (“phylogenetic repulsion” or “overdispersion”) implies competitive exclusion. This is a simple, novel, creative, and relatively easy-to-implement idea, and so it’s no surprise that it took off. Spurred by the increasing ease of building phylogenies, dozens of studies have now applied this “simple logical framework” to make inferences about coexistence mechanisms without the need for difficult and time-consuming experiments.
The problem is, this “simple logical framework” is wrong.* In fact, there are many reasons why phenotypically-similar species might coexist besides “habitat filtering”. Further, the idea of “limiting similarity”, which Webb et al. take for granted, is a zombie idea; it’s long since outdated. Modern coexistence theory tells us that competing species must always be both sufficiently similar in relevant respects, as well as sufficiently different in other relevant respects, in order to stably coexist. Specifically, species need to be sufficiently similar in what might be termed “overall competitive ability”: if species are different in the sense that one is inferior to the other, that difference promotes exclusion, not coexistence. Species need to be sufficiently different in ways that weaken interspecific competition relative to intraspecific competition, thereby conferring a relative fitness advantage on rare species (which by definition experience mostly interspecific competition) and allowing those species to “bounce back” rather than go extinct. For all these reasons and others, there’s no clear theoretical expectation about whether co-occurring species will be more or less phenotypically similar than expected by chance, and so no way to reliably infer contemporary coexistence mechanisms simply by mapping co-occurring species onto a phylogeny, no matter whether phenotypic traits are phylogenetically conserved or not. And so we probably shouldn’t be surprised that empirical studies find mixed results: phylogenetic clustering is most common, but overdispersion and randomness are not uncommon, and the determinants of clustering vs. overdispersion remain unclear (Vamosi et al. 2009). Other lines of empirical evidence, such as competition experiments among species of varying relatedness, also provide mixed results (e.g., Cahill et al. 2008). Obviously, there could be all sorts of reasons for these mixed results, but they don’t necessarily need any special explanation at all. Mixed empirical results are precisely what you expect if your hypothesis is unfounded in the first place.
None of the points in the previous paragraph are original to me. They’re made much better than I just made them by Mayfield and Levine (2010; hereafter M&L). Many papers (including, to their credit, Webb et al. themselves) discuss modifications, elaborations, exceptions, and qualifications to the core ideas of Webb et al. But M&L is, as far as I know, the first paper to argue that the core idea of Webb et al. is fundamentally flawed.
Which provides an opportunity for an interesting case study: What happens when you push back against a bandwagon? How do other researchers react? Do early reactions to the pushback provide any hints as to whether the bandwagon will eventually stop or be redirected, or whether it will continue on as if the pushback had never happened?
For reasons I’ve discussed before, bandwagons in science are difficult to stop or steer. But M&L have a number of factors working in their favor. They published in the highest-impact ecology journal in the world, Ecology Letters. No one has any excuse for failing to notice their critique. They’re both established researchers, and Jon Levine in particular is quite prominent, so people should read what they have to say and take it seriously. Their paper doesn’t use any math which might scare off some readers. And their paper has a positive as well as a negative element. They suggest that it would be very valuable to link modern coexistence theory to patterns of phylogenetic relatedness (although they suggest no simple recipe for doing this, because none exists). People are more likely to drop their current approach if you suggest an alternative.
Even if you don’t agree with M&L’s critique, I hope you’ll agree that this is an interesting case study of a contrarian attempt to stop or steer an ongoing bandwagon. You have a situation where lots of people are pursuing a particular question using a particular approach. But then someone well-known publishes a serious, easy-to-understand critique of that approach in a very prominent venue, and suggests an alternative approach. What happens next?
To find out, the first thing I did was to look up how often M&L have been cited. Has their critique in fact been widely noted, as you’d expect? As a baseline, I looked up how often Webb et al. 2002 (the paper that more or less founded this area of research) and Vamosi et al. 2009 (a recent major review of this area of research) have been cited since M&L was published. If lots of people are citing Webb et al. and Vamosi et al., but not citing M&L, that’s a sign that their critique isn’t being widely noted.
M&L was published in the September 2010 issue of Ecology Letters and has been cited 38 times since, according to Web of Science. In contrast, Webb et al. has been cited 211 times since Sept. 1, 2010. Now, Webb et al. discuss other ideas about phylogenetic community structure besides the idea critiqued by M&L, and so many of the citations of Webb et al. likely are for reasons independent of the M&L critique. But still, the order-of-magnitude difference here is striking. Vamosi et al. is a review of precisely the same topic critiqued by M&L, and so one might expect that most papers that have reason to cite Vamosi et al. would have equal reason to cite M&L. But Vamosi et al. has been cited 76 times since Sept. 1, 2010, twice as often as M&L. Of course, Vamosi et al. was published the year before M&L, and so some studies citing Vamosi et al. but not M&L likely were already in review or in press before M&L was published. But even if we restrict attention to papers published since Sept. 2011 (a year after M&L was published), we find that Vamosi et al. has been cited 41 times, and M&L only 27 times. So while M&L has hardly gone unnoticed, many papers which you’d think would have good reason to cite M&L don’t do so. Now, it’s possible some papers cite Vamosi et al. but not M&L for good reason; you’d need to read those papers in detail to find out. But it sure seems like there might well be some papers out there proceeding as if M&L had never been written. Which is a rather depressing possibility.**
But it’s not as if M&L have been ignored entirely; they’ve been cited 38 times in two years. Of course, not all citations are created equal; papers are cited for all kinds of reasons. So I skimmed each of the 38 papers citing M&L (in one case only looking at the abstract, as the full text wasn’t available to me) and classified them into categories based on how they cited M&L. In most cases, a paper fell into only one category, but in a couple of cases M&L were cited in different ways in different parts of the paper, so I included the paper in multiple categories. Applying this classification system obviously involved judgement calls on my part. But because I only used a small number of broadly-defined categories, there were only two ambiguous cases. And every paper fit somewhere in my classification scheme, except for one that I ignored because it was in Spanish and I can’t read Spanish. Here are the categories:
1. Papers that aren’t about inferring coexistence mechanisms from phylogenies. These papers cite M&L for various reasons, often for their review of modern coexistence theory and critiques of “limiting similarity”.
2. Papers that are about inferring coexistence mechanisms from phylogenies, that cite M&L only in passing. These are papers that cite M&L, but not so as you’d notice; they proceed more or less as if M&L had never been written. Some cite M&L by first citing Webb et al. and a bunch of other papers and then writing “but see M&L”. Others cite M&L in such a way that you wouldn’t know from the citation that M&L was a fundamental critique of the ideas of Webb et al.
3. Papers that are about inferring coexistence mechanisms from phylogenies, that cite M&L as one paper among many. These papers typically lump M&L in with other papers discussing elaborations, modifications, qualifications, or exceptions to the ideas of Webb et al.
4. Papers that are about inferring coexistence mechanisms from phylogenies, that specifically discuss M&L briefly.
5. Papers that are about inferring coexistence mechanisms from phylogenies, that discuss M&L at length. This category includes papers based on the ideas in M&L.
6. Papers that miscite M&L, for instance by citing them in support of claims that they themselves actually deny. I was conservative in deciding whether to classify papers into this category. Merely citing M&L in passing or in a vague way (e.g., as part of a long list of papers cited in support of some broad claim) wasn’t enough for me to list a paper here, even though such citations could leave an unknowing reader with a mistaken or vague impression of the content of M&L.
If M&L is having an impact on phylogenetic community ecology, you’d expect citations of it to mostly fall into categories 4 and 5. Papers in category 1 aren’t directly relevant for purposes of this post, but they’re indirectly relevant in a couple of ways. On the one hand, any recognition of the arguments of M&L, even in a paper that’s not about inferring coexistence mechanisms from phylogenies, presumably helps to increase awareness of M&L. On the other hand, insofar as papers citing M&L fall into this category, it means papers that are about inferring coexistence mechanisms from phylogenies aren’t citing M&L. Citations in category 2 suggest a bandwagon that’s rolling along more or less unstoppably. If most citations of M&L are in category 2, it suggests M&L will have roughly the same effect on phylogenetic community ecology as Clarence Darrow’s closing speech had on the outcome of the Scopes trial–i.e. little or none (H.L. Mencken wrote that “The net effect of Clarence Darrow’s great speech yesterday seems to be precisely the same as if he had bawled it up a rainspout in the interior of Afghanistan.”) Citations in category 3 don’t suggest lack of impact, exactly, although they do indicate that the authors don’t see M&L as distinct from papers suggesting modifications, elaborations, or caveats to Webb et al. (personally, I do see M&L as quite distinct, but I suppose the point is arguable). And whether or not M&L are having any impact, there shouldn’t be any citations in category 6. There’s no good excuse for miscitations.
Here are the numbers. In some cases, ranges are given because of a couple of ambiguous cases:
1 (papers on other topics): 18-19 papers
2 (cited in passing): 8-9 papers
3 (cited as one paper among many): 4-5 papers
4 (discussed briefly): 6 papers
5 (discussed at length): 3 papers
6 (miscited): 2-3 papers
These results surprised me. I expected that M&L would mostly have been cited in passing or as one paper among many—that it would be widely noted, but only in a relatively cursory way. But roughly half of all citations of M&L are by papers that aren’t even about inferring coexistence mechanisms from phylogenies at all. M&L is most often cited simply as a review of modern coexistence theory or as a critique of the idea of limiting similarity. In a way I think that’s good; anything that helps modern coexistence theory penetrate the collective consciousness of ecologists is good. But on the other hand, it means that papers about inferring coexistence mechanisms from phylogenies have only cited M&L about 18 times since it was published, compared to many more citations for papers developing or reviewing the ideas that M&L critique. That doesn’t seem to me like a bandwagon that’s going to be stopped or steered by M&L. It’s much like the pattern you see with the intermediate disturbance hypothesis, where the papers that originally developed the idea continue to be cited far more often than papers critiquing the idea.
As for the remaining categories, it’s unsurprising but a bit depressing to see category 2 (citations in passing) as the largest remaining category, comprising almost half of the remaining papers. On the other hand, I’m pleasantly surprised to see that papers that specifically discuss M&L (whether briefly or at length) collectively outnumber those which just lump M&L in with the many other papers that have discussed elaborations or modifications of the ideas of Webb et al. I had thought category 3 would be a big one but it’s not.
Probably the biggest cause for hope for an M&L fan like me are the three papers in category 5. Kuntsler et al., Hultgren and Duffy, and Anderson et al. are all based largely on the ideas of M&L. These authors are the first to take up the positive suggestions of M&L. I could see these papers having an impact. Often, the most effective way to critique an established approach is not to criticize it directly, but simply to do things differently, and show that doing things differently leads to novel insights that wouldn’t have been discovered under the established approach. I note with interest that all three were published in very high-profile journals (two in Ecology Letters, the other in Journal of Ecology). Usinowicz et al. in the latest issue of Ecology is another terrific example of a paper taking a different approach to link coexistence mechanisms and phylogenies (although phylogenetics isn’t the main focus of the paper, so it actually doesn’t cite M&L even though it’s thoroughly grounded in modern coexistence theory). Perhaps the phylogenetic community ecology bandwagon will start to change course as more ecologists begin to realize that following the lead of M&L is a good way to get a high-profile publication.
Our papers sometimes have their greatest impact in ways the authors never expected. My former labmate Jill McGrady-Steed did one of the first experimental tests of biodiversity-ecosystem function relationships (McGrady-Steed et al. 1997 Nature). At the end of the experiment, just for the heck of it, she tried invading all her communities with a species not used in the experiment, and found that the invader only invaded species-poor communities. That throwaway result on the diversity-invasibility relationship turned out to be the main thing people cited her for. Maybe M&L, and those who follow their lead, won’t end up having much impact on the phylogenetic community ecology bandwagon, but will end up having a big impact by helping to spread the word about modern coexistence theory. Which might prevent some future unfounded idea about how to infer coexistence mechanisms from ever being proposed in the first place.
Of course, there’s also the question of the impact this blog post will have. ;-)
*As always, in saying that Webb et al.’s idea is wrong, I imply no personal criticism of any of the authors. They’re all very smart and very good ecologists, and Mark McPeek in particular is a friend. But everyone makes mistakes, including serious ones.
**I am of course unable to quantify the number of papers that M&L prevented from being written or published. That is, perhaps some ecologists who might otherwise have written papers based on Webb et al. changed their plans after reading M&L, or perhaps they had their papers rejected by referees and editors convinced by the critique of M&L. But if I had to guess, I’d bet that the number of such papers is at most very small.