A while back, the ASN held a formal debate on whether species richness at continental scales is governed by ecological limits. The opposing papers–Dan Rabosky and Allen Hurlbert arguing in favor, Luke Harmon and Susan Harrison in opposition–came out in Am Nat a few months ago. I finally got around to reading them. Great stuff–there’s a lot to chew on here! Well worth reading even if you’re not all that interested in macroecology or macroevolution, because they comprise a terrific case study of science in action. For any question big and interesting enough to be worth asking, it’s often not obvious exactly what the question is, or how to answer it. It’s fascinating to see how different experts define a question and evaluate the evidence.
Below are thoughts inspired by the papers. I’m going to assume that you’ve read the papers, so go do that if you haven’t already (or if you’re lazy you can try to get by with Carolyn Tucker’s brief summary).
Don’t think of this as “post-publication review”. I’m very glad both papers were published and wouldn’t change a thing about them. And nothing I say is a personal criticism of any of the authors, all of whom I hugely respect. That I sometimes disagree with them just shows that disagreement is a normal part of science.
- A big part of the disagreement here is about what “limit” means.
I’m totally with Rabosky & Hurlbert on this one. Species richness is gonna vary over time. We don’t know of any reason why that wouldn’t happen, but we do know of lots of things that might impart some negative feedback or return tendency to that variation. So the sensible first-order question to ask is the one Rabosky & Hurlbert ask: is there any return tendency? That is, does continental scale species richness tend on average to increase from low values, and decline from high values? As opposed to, say, just tending to grow exponentially, except when mass extinctions knock it back. Or as opposed to doing an unbiased random walk (i.e. per-species speciation and extinction rates are equal on average, but are either constant over time or else vary independently of species richness). In contrast, I’m not sure exactly what Harmon and Harrison mean by “limit”. But they seem to mean either “species richness remains constant or nearly so, with only biologically-trivial amounts of variation”, or “species richness has a hard, extrinsically-imposed upper limit that can never be exceeded”. Assuming I’m not badly misreading them (and apologies if I am), I don’t like either of those ways of defining “limits”, for several reasons. First, it’s pretty easy to reject both, but doing so doesn’t teach you much because it still leaves you with a whole world of very different possibilities–including the one that Rabosky & Hurlbert consider. A world in which continental-scale species richness has a strong return tendency is a very different world, ecologically and evolutionarily, from one in which it has no return tendency at all–but neither is a world in which species richness doesn’t vary, or always stays below some hard upper limit. Defining “limits” as Rabosky & Hurlbert do doesn’t set the burden of proof for “limits” too low, it just frames the question so that it has an informative answer. Second, it’s a mistake to think that, because some variable of interest exhibits high temporal variance, or has ups and downs that are correlated with the ups and downs of some extrinsic driving variable, that it must have little or no return tendency, or that whatever return tendency it has is somehow unimportant. See Ziebarth et al. 2010 for an exceptionally clear discussion of this mistake in the context of population ecology. The strength of a variable’s return tendency, its temporal variance, and the fraction of its variation explained by variation in some extrinsic driver variable, are three very different things. They’re related, but often in the opposite way to how you might intuitively think. So I disagree with Harmon & Harrison when they claim the temporal variability of species richness in fossil time series data as evidence against Rabosky & Hurlbert. Any amount of temporal variability in a time series is consistent with any strength of return tendency. Third, I can’t think of any variable in biology that has a hard, extrinsically-imposed upper limit on its value, the way nothing in the physical world can move faster than the speed of light. In particular, it’s tempting but very misleading to think of “niches” as like houses that exist independently of species, so that once all the houses are filled no more species can live in that neighborhood. Species are not like Dr. Seuss’ nutches. The only constraints I can think of that impose hard upper limits on the values of biological variables are mathematical constraints. For instance, the species richness in some part of North America can’t be negative, and can’t exceed species richness in all of North America.
- This debate is just like the density dependence debate in population ecology–so can we resolve it the same way? Following on from the previous bullet, Harmon and Harrison note, correctly, that the debate here is just like the debate over density dependence in population ecology. Which is why it puzzles me that they define “limits” as they do. It’s actually Rabosky and Hurlbert who define “limits” analogous to how most population ecologists these days define density dependence. One thing Rabosky & Hurlbert’s way of defining “limits” has going for it is that it lets you bring modern statistical techniques of time series analysis to bear. So despite my puzzlement over Harmon & Harrison’s way of defining “limits”, I agree 100% with them that we ought to be as statistically rigorous as we can in testing for limits. Rather than just eyeballing time series of continental-scale species richness to see if they have any return tendency, we ought to be trying to estimate that return tendency statistically, for instance using the approach of Ziebarth et al. 2010 or Knape & de Valpine 2012. Not that this will be a panacea. Rabosky and Hurlbert quite rightly point out that the stationary distribution to which species richness tends to return can change over time (and also vary from place to place). And in response, Harmon & Harrison quite rightly point out that it’s very hard to distinguish a system without any return tendency from a system which has a return tendency but which tends to return to different stationary distributions at different times in its history. My suggestion is to start simple, as population ecologists have done. Start by looking at whether time series data on continental-scale species richness are best described by a model with a return tendency, that includes exponential growth and a density-independent random walk as limiting cases. Based on the results of that analysis, decide whether it’s useful to estimate something complicated, like a model with some sort of temporally-varying stationary distribution, or a model that switches back and forth between having a return tendency and lacking one. There’s precedent for this sort of approach in other contexts in paleontology, like Gene Hunt’s work asking which of several different time series models best describes trait evolution time series (Hunt 2007, Hunt 2008, Hunt et al. 2015). So now I’m very curious to dig into the paleontological literature to see what the state of the art is with regard to analyzing time series data on species richness or clade richness.
- The importance of checking assumptions as well as testing predictions. I love that both pairs of authors want to check both the predictions and the assumptions of the ecological limits hypothesis. Testing predictions is great, but ecologists often focus too narrowly on testing predictions, to the exclusion of checking assumptions (see here and here). Checking assumptions as well as testing predictions is how you distinguish between a model that’s actually right, and a model that’s just getting lucky.
- The importance, and challenge, of using microscale evidence to test macroscale hypotheses. I love that both pairs of authors consider various “microscale” lines of evidence, even though they’re ultimately interested in explaining macroscale data. They all agree that the macroscale is–has to be–the aggregate outcome of lots of microscale events. Just because you ultimately care about the macroscale doesn’t mean the microscale is somehow irrelevant or unimportant or ignorable. Rather, if your macroscale hypothesis makes microscale assumptions (and how could it not, at least implicitly), or makes predictions about microscale data, then you have to check those assumptions and test those predictions. But of course, as we’ve discussed in lots of old posts, scaling up from the microscale to the macroscale is really challenging (e.g., here and here). A lot of the disagreement between the two sides seems to come down to disagreement about what, if anything, various lines of microscale evidence imply about the macroscale hypothesis Rabosky & Hurlbert defend. I won’t comment too much on that, except to say that…
- I disagree with Harmon & Harrison on local-regional richness relationships. One line of microscale evidence both sides discuss are data on how the species richness of local communities relates to the richness of the “regional species pools” from which those local communities were presumably assembled. I’m totally with Rabosky & Hurlbert on this one–you cannot infer anything about whether or not local communities are “saturated” with species, or even whether species interactions have any appreciable affect on local species richness, by looking at plots of local vs. regional richness. I think that’s a zombie idea–see this old post. (Aside: that post is based on two recent meta-analyses of local-regional richness data, neither of which is cited by these two papers.)
- I think I disagree with Rabosky & Hurlbert on how island biogeography models work. This is a small and possibly-pedantic point. Rabosky & Hurlbert describe their hypothesis as analogous to simple models of island biogeography. They say that, in simple island biogeography models, the fact that there is some stable equilibrium value of island species richness towards which the system tends is a reflection of finite resource availability. I don’t think that’s right. The fact that simple island biogeography models have a stable equilibrium value of species richness reflects the assumption that there’s a fixed, finite number of species on the mainland. Consider a system in which there are P species on the mainland. They colonize the island at some constant per-species rate c that’s the same for all species. The island has S species. The probability that a newly-arrived species is not already present on the island, thereby increasing island species richness, is 1-S/P. Species on the island go extinct at a constant per-species rate e that’s the same for all species. These assumptions imply that the rate of change of species richness on the island is dS/dt=cP(1-S/P)-eS. That equation has a single equilibrium, S*=cP/(c+e), and that equilibrium is globally stable. It’s not globally stable because of any resource-based limit to how many species can colonize the island, or because per-species extinction rates increase with island species richness due to resource competition. It’s globally stable because, the more species there are on the island, the lower the odds that any colonist is a new species. That’s not to say that resource limitation sensu Rabosky and Hurlbert doesn’t occur or isn’t important. My point is a conceptual one–you don’t need that sort of resource limitation to have a stable equilibrium value of species richness in an island biogeography model. Of course, maybe you do need resource limitation or something that does the same job in the context of the macroecological/macroevolutionary speciation-extinction model Rabosky & Hurlbert propose. Since in those models, speciation, not a fixed mainland species pool, is the ultimate source of diversity.* Anyway, I wanted to raise this because I’m always puzzled and surprised when I discover that even experienced ecologists sometimes don’t mean the same thing when they refer to some very basic textbook model or concept.
*In fact, the total rate at which new species colonize doesn’t even need to decline with increasing island species richness for the island to have a stable equilibrium species richness. For instance, consider the model dS/dt=x-eS, where x is some constant rate at which new species arrive on the island. Doesn’t matter from where; it doesn’t have to be from a mainland with some fixed number of species on it. Could be that, once per unit time, the Flying Spaghetti Monster (or an experimenter!) adds one or more new species to the island. That model has a globally stable equilibrium island species richness, S*=x/e. It’s globally stable because the per-species rate at which new species colonize is x/S, which of course declines with increasing S. This model is “density dependent” in the same way that population ecology models with a constant rate of immigration are density dependent. There are ecologists who would regard this sort of “apparent” density dependence as some kind of trivial or misleading artifact, but I don’t think it is. It’s just a different mechanism giving rise to density dependence. Now, fair enough if you don’t think this is a realistic island biogeography model; I don’t think it’s realistic either. But don’t let that blind you to the conceptual point. You don’t have to have resource limits to have a stable equilibrium species richness on an island (well, unless you want to argue–debatably–that without resource limits no species would ever go extinct, so e=0).
“So now I’m very curious to dig into the paleontological literature to see what the state of the art is with regard to analyzing time series data on species richness or clade richness.”
Well, I think there’s a lot of work in this area… as far as fitting models to the diversity curve itself, off the top of my head, I think of Alroy 2009 (https://www.nceas.ucsb.edu/~alroy/pdfs/2009-Speciation.pdf) or Marx and Uhen 2010 (https://www.sciencemag.org/content/327/5968/993). Many studies take a much more detailed view than just diversity counts, digging into origination and extinction rates and trends across individual clades, like Quental and Marshall 2013 (http://www.sciencemag.org/content/341/6143/290.short) and Silvestro et al. 2013 (http://www.pnas.org/content/112/28/8684.short).
Cheers for that. At a quick glance, those papers are doing something slightly different (not better or worse, necessarily, just slightly different) than what I had in mind. Those papers seem to be trying to estimate speciation and extinction rates, and diversity-dependence thereof. I was thinking of looking at diversity-dependence of the net diversification rate, by just analyzing the species richness time series. Analogous to how, in population ecology, we usually start by looking for density dependence of per-capita growth rate by just analyzing the abundance time series. Rather than looking at time series of births and deaths. Although in population ecology, we generally don’t have data on births and deaths, which dictates the analytical choice here.
Er, Alroy’s simulating analyses in the 2009 paper is fitting to the paleo-diversity estimates (starting on page 313), and Marx and Uhen are also fitting to the paleo-diversity curve, not origination and extinction, using an AIC framework very similar to Gene’s time-series analyses.
Also see Graeme Lloyd’s 2012 paper (http://rsbl.royalsocietypublishing.org/content/8/1/123). A lot of the time-series analysis of diversity counts is to look for correlations to time-series of various sampling proxies and various paleoenvironmental measures. Here’s a very recent example of this: http://www.nature.com/ncomms/2015/150924/ncomms9438/full/ncomms9438.html
Ah, I clearly glanced too quickly at those papers! Thank you; I’ll read them more thoroughly so that I know what I’m talking about before commenting further. 🙂
The Alroy paper Dave cites is perhaps the most directly related to this debate. By focusing on one continent (North America) he shows that the variance in richness through time is much less than a brownian motion process would predict. Of course, it’s limited to one clade, because in the terrestrial realm, mammals are about the only group where this kind of plot is really possible (maybe pollen, but then there are issues of species identification…)
Silvestro et al also just had a paper out in PNAS looking at origination/extinction rates in North American carnivorans and found strong evidence that certain clades suppress the diversification of others. Likewise, Liow et al just had a paper on clams and brachiopods that found that brachiopod origination rates are stymied by bivalve diversity. Again, both are a bit more removed from the specifics of the debate (total local/regional/continental richness), but both also support the idea that the fossil record is in agreement with diversity limits.
With regards to microscale processes, I guess I have a hard time fitting the Harmon & Harrison paradigm with observed levels of adaptation. It’s unclear to me how you get selection for improved resource acquisition over large geographic ranges in the face of drift and gene flow without resource limitation *also* mattering over large geographic distances. E.g., some snakes have venom conducting teeth, but they had to evolve those in response to selection, and the only way selection works is if *some* of those snakes failed to acquire enough resources to reproduce sufficiently often to offset the reproductive gains made by snakes that *did* have the adaptation. That differential in resource-to-reproduction had to hold over a large enough area that drift and gene flow from less specialized subpopulations were unable to swamp it out. Basically, a world in which there are no limits (or we’re so far from the limit as to not matter) strikes me as a world in which selection on terrestrial organisms is utterly ineffective.
“Basically, a world in which there are no limits (or we’re so far from the limit as to not matter) strikes me as a world in which selection on terrestrial organisms is utterly ineffective.”
Hmm…not sure about that. All selection cares about is relative fitness. You can have variation in relative fitness in a density-independent world.
You’re probably correct, that was just my knee-jerk response to the argument. My rationale would be better put as something like this:
Under a nonlinear functional response for predators (such that large prey abundances do not necessarily beget infinite predator abundances), resource consumption is not zero-sum in a prey-unlimited world. Predators with allele A’ may not actual gain much of a fitness advantage of predators with allele A unless the allele changed the actual shape of the functional response, such that the predator responds better to high prey abundance. Which I guess is possible, it just seems to my intuition (always dangerous to use) to make it a bit harder to generate large differences in relative fitness if you remove resource limitation.
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