I’m a bit late to this, which is embarrassing because I was involved in it. Back in May, Functional Ecology published a special feature (well, they call it an “extended spotlight”) on community phylogenetics. I helped edit the special feature, along with Anita Narwani, Patrick Venail, and Blake Matthews. Here’s our introductory editorial, which basically argues that phylogenetic community ecology has gone too far down the well-trodden
road dead end of trying to infer process from pattern and that it’s high time for a course correction.
If it sounds rather like some old blog posts of mine (e.g., this and this), well, that’s no accident. It’s because of those old posts that Anita and Patrick invited me to join the team (they were the driving force behind this, having organized the symposium this special feature grew out of). So there’s a tangible benefit of blogging to add to the rather short list–you might get mistaken for an expert and invited to edit a special feature. 🙂 That my involvement in this project grew out of my blogging is my tissue-thin justification for posting about it.
The four papers in the special feature are quite different in terms of the specific topics addressed and the approaches used to address them. But they’re all nice examples of contrarian ecology, pushing back against the current conventional wisdom.
Kraft et al. use modern coexistence theory to rethink and make precise the disturbingly-popular-for-such-a-vague-idea notion of “environmental filtering”. They then review the literature and find that most studies of “environmental filtering” don’t actually present evidence of environmental filtering, properly defined. They argue that current vague usage of the term overstates the importance of abiotic tolerance in determining community composition. A nice example of something I’ve been thinking about a lot lately–how attempts to quantify vague concepts often just paper over the vagueness, leading to confusion rather than insight. One consequence of their argument (which I agree with 100%, btw) is to undermine a recently-proposed method for generating simulated datasets structured by a specified strength of environmental filtering. Which is kind of a funny coincidence, because the lead author of that method also wrote one of the papers in this special feature.
Gerhold et al. challenge the idea that the phylogenetic relatedness of co-occurring species can be used to infer the mechanisms driving community assembly. They point out that this idea depends on numerous strong assumptions that are weakly supported at best. They suggest more useful things that ecologists can do with phylogenies besides trying (futilely) to use them as a convenient shortcut to discovering community assembly mechanisms.
Venail et al. show, contrary to some recent claims, species richness, not phylogenetic diversity, predicts total biomass and temporal stability of total biomass in BDEF experiments with grassland plants.
Finally, Münkemüller et al. use evolutionary simulations to show that commonly-used measures of “phylogenetic niche conservatism”, such as phylogenetic signal, actually are very hard to interpret, and often are highly misleading guides to the underlying evolutionary processes governing niche evolution.
It will be interesting to see if these papers have much impact. I predict that Venail et al. will. It’s a comprehensive review of a purely empirical topic, and so I think it will quickly become the standard reference on that topic. The impact of Münkemüller et al. is harder to predict. My guess is it’ll get cited in passing a lot, but that people will mostly keep doing what they’ve been doing on the (dubious) grounds that there’s no easy alternative. I think Gerhold et al. and Kraft et al. will have little impact, unfortunately. They’re telling community ecologists to abandon an easy-to-follow recipe that purports to allow inference of process from pattern. Community ecologists only reluctantly abandon such recipes. But a minority of ambitious community ecologists will recognize that there’s an opportunity to do really-high impact work by following the lead of Kraft et al. rather than by following the crowd.
The editorial and the papers are open access, so check them out.
I know you are very passionate about this debate, Jeremy, and have informed us on many relevant points about it. While I do not have the depth of understanding you have on this particular topic, if I accept what you endorse at face value, then yes, it would seem the work concerning phylogenetics & community structure is on shaky ground.
But I do not necessarily believe a push of the pendulum in the other direction (i.e., abandoning all pattern to process work) in community ecology is warranted. Even though it appears this particular thread of investigation has reached a “dead end,” there appears to have been value in applying this philosophy:
The Concept of Pattern in Ecology; G. E. Hutchinson
Proceedings of the Academy of Natural Sciences of Philadelphia; Vol. 105 (1953), pp. 1-12 .
The Paradox of the Plankton; G.E. Hutchinson; American Naturalist; Vol. 95 (1961), pp. 137-145.
I realize these papers are just a wee bit outdated, and certainly the principles of competitive exclusion and niche have undergone substantial modification since the time of Hutchinson & his cohorts. Nonetheless the ideas of this generation propelled ecology into an age of mathematics that continues on in the current day. While the pattern to process inferences of this generation may not have been as precise as they once thought them to be, they most certainly pushed ecology into the realm of quantification.
Unless I misunderstand, Jeremy, you seem to argue for a complete abandonment of pattern to process work. I believe that would remove a potentially valuable approach from our toolbox, and so I do not concur if indeed that is your position.
There are contexts in which inferences from pattern to process are reasonably reliable. Inferring the causes of population cycles, for instance–see the work of Bruce Kendall, Ed McCauley, & their collaborators. Inference from pattern to process is reasonably reliable in that case because the pattern (e.g., the period and amplitude of the cycles) is extremely informative. It’s quite difficult to reproduce the pattern with the wrong processes–only the right processes will work. Unfortunately, that is not true for the vast majority of cases in ecology.
Hutchinson quite rightly called ecologists’ attention to various features of nature that need explaining. The question is how you go about explaining them. Trying to “read off” the explanation for a pattern directly from the pattern itself almost always fails in ecology.
Yes- the work of Kendall & McCauley is exceptional. The pit I find many people falling into is the use of weak inferences. I’ve observed ongoing debates about the issue of correlation, for example. There does not appear to be a consensus on what a weak v. strong correlation is, and I have discovered many investigators arguing for pattern to process when their data are sketchy at best. Often what you hear is, for example, a correlation of 0.5 or 0.6 is really very good, because so many variables affect any given relationship that you are fortunate to realize this level of significance. The other issue here relates to the error limit one applies, and this is discussed in depth by Elzinga, Salzer & Willoughby 2001 (measuring & Monitoring Plant Populations, 496 p.).
And so I believe a big part of the problem you mention is tied to the practice of applying relatively weak correlations and liberal error limits to explain process. That opens the door to profound confusion, because simply saying there are an unknown number of variables effecting the system which you have not measured, and then arguing your data explain it, is reckless science. Thus I advocate cleaning up the science and not throwing the baby out with the bath water because of decades of sloppy science.
These papers are great, and I’ve been working through ’em.
They really get at this weird assumption that’s always bothered me. Specifically, this idea that we actually have good models for trait evolution along phylogenies that are easy to fit. No one thinks Brownian Motion is how traits really evolve, but things like “phylogenetic signal” all assume it is. The entire idea that two recently diverged lineages will have a “hard time” coexisting is based on the assumption that their traits are especially similar, which comes straight out of Brownian motion.
Really, we need to better integrate ecological and evolutionary theory together to more robustly model these sorts of dynamics. Currently, all evolutionary models assume that species are perfectly dependent before divergence (true) and perfectly independent after divergence (potentially catastrophically untrue). Whether two sister lineages occur on different continents or in the same vernal pools has no bearing on any commonly used model of trait evolution, which seems crazy.
Basically, all the comparative models we use “do” is describe facets of patterns. Ornstein-Uhlenbeck patterns do not suggest adaptive evolution, rather they only suggest that the divergence between lineages is much greater relative to the total divergence of the clade than other models would predict. Which could be produced by rampant ecological character displacement or stabilizing niche differences a la Kraft’s paper above driving up rates between close lineages, or functional/developmental constraints limiting the total divergence possible for the clade and making the divergences between closely related species *seem* high. Or probably a whole bunch of other processes that have nothing to do with adaptive peaks that we haven’t thought of yet.
We either need really holistic models that incorporate dynamics from ecological *and* evolutionary theory to test our pet ideas directly, or we need to focus on more robust descriptions of patterns (better indices, to call-back to your post the other day) in the hopes of testing those good descriptions against specific models that should predict them. Both seem like productive routes to a lot of really interesting science, and both are being pursued by folks already, but I find it really unsurprising that the current simple descriptors of traits-on-trees, like ‘phylogenetic signal’, fail utterly at discriminating between ecological processes.
Good comments. I share your concerns, and your ideas about the way forward. Thought I’m rather pessimistic about “really holistic models that incorporate dynamics from ecology and evolution”. But it’s not really my field, so perhaps I’m not the best judge of the most promising way forward.
I wonder if experimental studies of contemporary organisms, like the Kraft et al. 2015 PNAS paper I linked to, have a role to play here. Seems like that sort of information ought to inform the evolutionary stories we try to tell. Though I suspect it’s going to be hard to tell a convincing eco-evolutionary story about the history of any group of organisms that’s not isolated on islands, with fairly simple ecology. Anoles and Darwin’s finches (our two best examples of integrating ecology and evolution to understand the evolutionary history of a phylogenetic group) are model systems for a reason.
That so many experiments have failed to find phylogenetic signal in the strength of competition in both pairwise and polyculture scenarios speaks volumes of the utility and generalizability of this approach (and has led me to largely abandon it in my own research).
Estimation of extinction rates from molecular phylogenies seems like a similar example of phylogenetic information being stretched too thin and relying on far too many unrealistic assumptions.
Preach on! I’m with you 100% on both those points.
I’m curious if it’s your sense that others working on these topics feel the same as you. Is it your sense that lots of people working on these topics share your views or are coming around to them?
I have an inkling that fewer people are publishing this type of analysis unless they have results more substantial than the typical over-under-dispersed patterns. Some of the noteworthy research I’ve recently seen involves 1) checking the assumption of habitat conservatism within different taxonomic ranks or lineages of different ages and 2) problems involving the delineation of the “regional pool.” Note that these studies are using the NRI/NTI metrics as a way to confront an assumption of the approach, rather than elucidate a particular mechanism.
The number of arbitrary decisions and jumps in reasoning one must make to then defend one mechanism over another seems too fallacious for me to take seriously anymore!
Haven’t seen the special issue yet, but am looking forward to it. I think (hope?) it’s become clear that trying to identify assembly mechanisms ONLY from phylogenetic pattern is, unsurprisingly, not a reliable way to go. There are more sophisticated ways, though, in which phylogenetic community data can be combined with other data to test hypotheses more rigorously. We did some work hybridizing phylogenetic-community patterns with species distribution models, and that’s one possibility (blog summary http://wp.me/p5x2kS-F; those highly motivated can chase down the paper from there). It is often true (and this is consistent with Brian’s recent post) that a simple idea like phylogenetic clustering/overdispersion spawns a rush, and only much later does it get properly thought out with sophisticated theory and methods for analysis. Stability/complexity, or limiting similarity, anyone? 🙂
I agree Stephen. I’d only add that the cases that come to my mind in which phylogenetic information was effectively combined with other information to tell a convincing, integrated story about the current and historical ecology and evolution of some system are cases like Darwin’s finches and Caribbean anoles. Unfortunately, I don’t know that that’s the kind of story most ecologists have been aiming to tell by latching on to phylogenetic data. It’s not a matter of just needing a theory or analytical method more sophisticated than phylogenetic overdispersion/underdispersion. It’s a matter of one’s goals. Gerhold et al. talk about this.