This post is the second in my series on mathematical constraints in ecology. In part 1 we saw an example of a non-obvious mathematical constraint that can’t be removed from one’s data. Today, an example of a mathematical constraint that’s totally obvious, but that has non-obvious consequences. And that fortunately can be removed from one’s data (well, worked around). Today’s topic is one I’ve posted on before, but I’m revisiting it for my ongoing comparative study of mathematical constraints in ecology and what to do about them.
Here’s a big ecological question: Is local species richness limited by local species interactions, so that sufficiently species-rich local communities are “saturated” with species? Or are local communities always open to colonization by whichever immigrants happen to arrive from the surrounding area, so that local species richness (and composition) is basically just a random draw from the regional “species pool”? For a while now, a popular way to try to test these alternative hypotheses has been to plot the richnesses of local communities vs. the species richnesses of the surrounding regions, and then fit competing regression models to the data. The idea is that a saturating curve (a line that goes up but asymptotes, like a type II functional response) shows that local communities in richer regions are saturated with species. Whereas a straight line with no asymptote shows that local communities are just equal-sized samples from the regional species pool. Each locality in the dataset just contains X% of the species from its surrounding region, on average. Most applications of this approach find linear local-regional richness relationships, which has been taken as evidence for a big general conclusion: local species interactions usually don’t matter.
All this is very intuitively appealing. When it was first proposed, it was a clever idea well worth pursuing and further developing. It’s in several undergraduate ecology textbooks now. Unfortunately, it turns out it’s wrong; I’d say it’s now a zombie idea. Theory and experiments show that it’s based on faulty intuitions. It’s easy to get a saturating relationship in a model with no local species interactions (Fox and Srivastava 2006). Conversely, you can easily get a linear relationship even when species interactions severely limit local richness by preventing colonization by species not present locally (Shurin 2000, Shurin et al. 2000). And that’s without even getting into all sorts of other technical issues and potential artifacts (Hillebrand 2005). Sadly, this turns out to be yet another failed way to infer process from pattern.
To which some “pattern first” readers might respond “But, the observational data! There’s a pattern there! There must be some interesting biological reason why most local-regional richness relationships are linear!” That response is wrong, because it’s based on a false premise. Most local-regional richness relationships are not linear. They only appear to be mostly linear because of a mathematical constraint.
The mathematical constraint is that local species richness can’t exceed regional richness. A locality is part of the surrounding region, so it can’t contain more species than the surrounding region. So a regression of local richness on regional richness necessarily occupies a bounded operational space: all the data, and the true local-regional richness relationship you’re estimating from the data, have to fall on or below the 1:1 line. It turns out that biases the results of standard regressions in favor of finding linear relationships (Szava-Kovats et al. 2011). When you correct this bias using what Szava-Kovats et al. call a logratio regression, you find that linear and saturating local-regional richness relationships are equally common in published datasets (Gonçalves-Souza et al. 2013, Szava-Kovats et al. 2013). And nobody’s been able to find an explanatory variable that differentiates the ~50% of systems with linear relationships from the ~50% of systems with saturating relationships. So there’s no empirical pattern here, and no theoretical reason to expect one (indeed, there’s good theoretical reason to expect a lack of pattern). Which as I argued in that old post means there’s no longer any reason for anyone to care if the local-regional richness relationship is linear or saturating. Much less try to infer anything from its shape. The idea should be dropped from the textbooks. (Aside: To be clear, there are still plenty of reasons to study beta diversity and scale-dependence of diversity more broadly.)
This is a good example of a mathematical constraint creating an artifact that can and should be corrected for. It’s also an interesting example of a constraint that was universally recognized, but that has consequences that long went unrecognized. In future posts in the series, we’ll see some examples of mathematical constraints that aren’t widely recognized (in some cases because they may not really be “constraints” at all). And we’ll see examples of mathematical constraints that, far from being nuisances, actually lead to profound biological insights.
Dynamic Ecology 
Thanks for this post Jeremy. I hadn’t kept up on the most recent literature on this (described in your next to last paragraph) which seems worth a look.
The whole notion of saturation has always seemed problematic to me. Saturation is really just a code word for species interactions limiting membership. But it is not obvious why species interactions could only limit membership rather than create new niches. There is ample evidence back to Paine that a predator can increase species richness at local scales. And in the latitudinal gradient there is a strong argument (although little empirical data) that biotic interactions increase richness (albeit this argument is usually made at a different spatial and temporal scale). The argument that species interactions could only cause a decelerating function vs community richness for odds of membership always seemed very handwavy (and excessively focused on competition) to me.
In my own local-regional richness paper, I included all species, not just competitors (Fox et al. 2000: http://homepages.ucalgary.ca/%7Ejefox/Fox%20et%20al%202000%20ELE.pdf). But yeah, that was unusual.
“Saturation is really just a code word for species interactions limiting membership. ”
As I think I said in the comment thread on that old post, for a while now I’ve wondered how much the popularity of this approach (which I do think has faded now, btw) depended on the fact that the same word (“saturating”) can be used to describe a regression that rises to an asymptote, and a community in which all the “niches” are “filled”. That the same word describes both things maybe helps fool you into thinking that they’re really one and the same thing. That a saturating regression is somehow synonymous with a saturated community.
Cool series of posts, JF. I thought I chopped the head of this zombie (however clumsily) in my first attempt at a quantitative paper as a second year graduate student (*cringe*). Jeez, these things are hard to kill (especially if you publish in a little-known journal).
DOI: http://dx.doi.org/10.1556/ComEc.2.2001.1.4
For an early draft of this post, I was planning to do a systematic review of the recent literature to see how many papers are still being published supporting this zombie idea, vs. how many cite Szava-Kovats et al. and Goncalves-Souza et al. I ran out of steam, though I can tell you that those two papers are very little cited so far. Which can’t be chalked up to publication venue, since both were in pretty widely-read journals.
FWIW, my sense from glancing at the recent literature is that this idea is going the way of the IDH–becoming a ghost rather than a zombie. Local-regional richness relationships got into some of the textbooks on the grounds of its early popularity and (apparent) success, even as theoretical and now empirical/statistical criticism mounted. Probably a lot of people who never really worked on the idea or followed the literature closely have the vague impression that it’s basically right (if so, very much like the IDH in that way). Meanwhile, the leading-edge literature seems to be moving on (again, very much as with the IDH). My very quick skim of the recent literature may well have missed some papers, but I don’t get the sense that leading journals are publishing many papers just trying to make inferences from local-regional richness relationships any more. If those sorts of papers are still being published, it seems like it’s mostly in obscure, unselective journals. Finally, Howard Cornell and Susan Harrison, probably the leading advocates of local-regional richness relationships, haven’t given up on the idea as best I can tell. But in their recent review/perspective-type pieces they seem to be moving towards a broader emphasis on “species pools” as an important object of study.
The cases of the IDH and local-regional richness relationships aren’t totally comparable, though. The timespans are different–the IDH took much longer to go from popular idea to zombie to ghost. And it’s my sense that local-regional richness relationships were subjected to a more steady drumbeat of criticism starting from pretty early on, including high-profile criticism (think of Diane Srivastava’s work from the late 90s). Whereas I think the IDH got a long way before there was much pushback.
I agree with all of this. We’ve also talked about how quickly the idea that you can infer processes (such as neutrality) from the shape of species abundance distributions also got pushed back on pretty quickly never gained mainstream momentum (although certainly never died).
I wonder if we’re getting better at critiquing ideas?
“I wonder if we’re getting better at critiquing ideas?”
Hmm, maybe? We’re talking small sample sizes here. It would be a challenging but interesting exercise to try to expand the sample. Is it the case that flawed ideas now have a harder time taking off than they used to, or get weeded out faster than they used to?
Can’t recall ever seeing data on this. Widespread complaints about the persistence of false ideas only ever complain about the current state of affairs as compared to some (unspecified) absolute standard. “Too many” flawed ideas persist in the literature for “too long”.
Time has a way of putting things into a new perspective. Our paper (and Goncalves-Souza et al.) left the message that many of the local-regional relationships in earlier work had been misdiagnosed. In this respect, we killed a zombie, but left a ghost. I think if I were writing the conclusions of this article today, I would suggest a problem lies in that such diagnosis was made at all.
I agree. Unfortunately, in practice it’s very difficult to prevent ecologists from taking up intuitively-appealing ways to infer process from pattern. Lately, I’ve tried to do it by shifting the burden of proof. The history of ecology is littered with promising-seeming but failed methods of inferring process from pattern. So any newly-proposed method for inferring process from pattern should face very strong skepticism by default. Unless and until the method has been proven to work.
“any newly-proposed methods of inferring process from pattern should face very strong skepticism” – but a key issue in inferring process from pattern is whether the method is looking at a single pattern (e.g., SAD, and as it became clear, single patterns are rarely diagnostic about underlying processes) or at multiple patterns simultaneously (e.g., SAD, SAR and many others). e.g. Hurlbert and Stegen 2014 Frontiers in Genetics on latitudinal diversity gradients. That requires of course that any given explanation of patterns is able to make predictions about all of those, which is not always easy/doable.
Oh, absolutely, I’m all in favor of testing more independent predictions rather than fewer. If you can do that, you have some chance of inferring process from pattern. It all comes down to the need for a 1:1 mapping of process and pattern. Each process or combination of processes of interest needs to lead to a unique pattern or combination of patterns.
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