The local-regional richness zombie is one I’ve mentioned in passing in various posts, but to which I’ve never actually devoted an entire post. It’s time to change that, thanks to the publication of an important new paper by Gonçalves-Souza et al. (forthcoming at Oikos; UPDATE: link fixed).* They’ve just taken a heck of a shot at killing off this zombie.
UPDATE: As a commenter notes, Szava-Kovats et al. (forthcoming at Ecology) was published online two days earlier than Gonçalves-Souza et al. and used the same approach to reach the same conclusions. I was aware of both papers, having reviewed them both, but hadn’t realized that Szava-Kovats et al. had just been published online too. For the record, Gonçalves-Souza et al. was actually accepted by Oikos before Szava-Kovats et al. was submitted. But I really don’t think priority should be the focus here. Certainly, in focusing my post on Gonçalves-Souza et al., I did not mean to try to confer priority on them, and I certainly didn’t mean to slight the equally-fine work of Szava-Kovats et al. The important thing is that both groups, working independently of one another, reached the same conclusions using the same methods. I find that reassuring. It’s not a given that two independent reviews of the same literature will reach the same conclusions. Think of recent competing meta-analyses of the diversity-productivity relationship, or further back the famously somewhat-contrasting reviews of field competition experiments by Schoener 1983 and Connell 1983.
Over at Oikos Blog, Gonçalves-Souza et al. have a fun summary of their paper which flatters me by placing their work within my own zombie-slaying tradition. I assume this is how a superhero feels when first joined by a sidekick. 😉 But after you click through and read their post, come back here and see what I have to say, because I’m going to draw some larger lessons about research programs in ecology and how they can avoid pursuing zombie ideas.
Briefly, the local-regional richness zombie is a shortcut (and you know what I think of those…). The idea is that, by plotting the species richness of local communities against the species richness of the regions in which they’re embedded, you can infer whether local species interactions are strong enough to limit local community membership. Here’s the argument. Species within any local community (a lake, a patch of grassland, whatever) typically didn’t speciate there. Instead, they colonized that local site from somewhere else, presumably from somewhere in the surrounding “region” (the regional “species pool”, if you like). Of course, not all colonists necessarily succeed in establishing a local population. In particular, they might fail because they get competitively excluded by other species. So local species richness reflects both the influence of the surrounding region (the source of colonists), and local conditions that determine the fate of colonists. How can we tease apart the relative importance of regional-scale and local-scale factors in determining local species richness? Why, by going out and sampling the species richness of local communities in different regions, and the richness of those regions, and then regressing local richness on regional richness. If we get a saturating curve (i.e. a curve that asymptotes or seems to be approaching an asymptote), then that means that local communities in sufficiently-rich regions are “saturated” with species.** All the niches are occupied and local competition prevents further colonization, setting an upper limit to local richness no matter how many species there are in the regional “species pool”. Conversely, if the local-regional richness relationship is linear, that means that local competition is too weak to limit local community membership. Instead, local communities are just samples of the regional species pool. Local communities just contain some constant fraction of the species from the surrounding region, with that fraction reflecting colonization rate. Lots of people have tried this idea out in their own systems–including me! (Fox et al. 2000)
Now, I’m sure you can imagine many potential problems with this approach. And you’re right to imagine problems. One big problem is that there are all sorts of confounding factors that will affect the shape of the local-regional richness relationship, but have nothing to do with the strength of local species interactions, colonization rates, etc. Differences among regions in environmental conditions and evolutionary history, to name just two. Another big problem is how to define “local” and “regional” scales, especially when localities and regions lack natural borders. Define either or both scales incorrectly (and how could you tell if you got them right?), and you’ll likely get the wrong answer. A third big problem is that the basic intuition behind this whole approach doesn’t stand up to scrutiny. There’s actually no reason to expect a connection between the processes determining local species richness and the form of the local-regional richness relationship. For instance, you can get linear or saturating local-regional richness relationships from a dead-simple model that lacks any local species interactions whatsoever, just by tweaking model parameters (Fox et al. 2006). For further review of the many obstacles to interpreting local-regional richness relationships the way most people have interpreted them, see Srivastava (2002), Hillebrand (2005), and other recent reviews.
Now, the numerous attacks on local-regional richness relationships as a shortcut to insight haven’t been ignored. But they certainly haven’t caused people to give up on the idea. My experience as a reviewer of many papers on this topic is that the issues reviewed above are acknowledged, but often only at the behest of reviewers, and usually only in passing. Basically, many authors take the view that, while looking at local-regional richness relationships isn’t a perfect way of inferring the determinants of local species richness, no approach is perfect, so we should just push ahead with what we’ve got and see what we find. Authors taking that view find it reassuring that a pattern does seem to emerge: local-regional richness relationships mostly are linear, and that seems to be true no matter what system you study. Indeed, to a certain sort of ecologist, a repeated pattern is in and of itself a strong reason to keep pursuing any research related to that pattern.
Trouble is, the apparent “pattern” is a statistical artifact. There is no pattern. As Gertrude Stein once said of the city of Oakland, “There is no there there.“
Let me explain. The standard way to test for linear vs. saturating local-regional richness relationships is to test whether a quadratic regression fits the data better than a linear regression. But the problem with that approach is that the “operational space” for the regression isn’t unbounded. By definition, a local site within a region can’t contain more species than the region. So all local-regional richness relationships, linear or saturating, are constrained to fall below the 1:1 line. Now, if observed local-regional richness data always fell well inside the boundaries of the operational space, maybe the boundedness of the operational space wouldn’t be a problem. But in practice, at least some observed data points in most datasets fall close to or on the boundaries of the operational space.
In a big statistical advance, Szava-Kovats et al. (2011; I handled it as an editor at Oikos) came up with a clever way around this by means of a logratio transformation, so that the regression can be conducted in an unbounded operational space. Now, I wouldn’t necessarily call logratio regression “the” right way to analyze local-regional richness relationships. Bounded operational spaces are tricky to deal with statistically and I don’t think there’s any universal “recipe” for how to deal with them. But I do think logratio regression is a clear improvement over conventional regression here–it gives you more interpretable answers without being any more difficult to implement (statistical machismo, this ain’t). Szava-Kovats et al. applied their new logratio regression approach to a few illustrative examples, showing that it changes the conclusion in some cases.
Now Gonçalves-Souza et al. have taken the next step and gone back through the literature reanalyzing every published local-regional richness relationship they could find using this improved statistical approach. It turns out that the apparent prevalence of linear local-regional richness relationships is an artifact of conducting linear regressions in a bounded operational space. 70% of published local-linear richness relationships look linear when analyzed by conventional regression–but only 53% do when analyzed with a logratio regression, with the other 47% being saturating. Fully 40% (!) of published local-regional richness relationships are misclassified by the conventional regression approach. Indeed, some of the most famous and widely-cited “textbook” examples of “linear” local-regional richness relationships actually are saturating. Which is unfortunate, given that these “textbook” examples literally are in the textbooks!
Now, if you’re attached to local-regional richness relationships as a shortcut to insight into the determinants of local species richness, you might respond by saying something like the following. “Ok, but that just changes the question from explaining a pattern to explaining variation. We need to figure out why about ~50% of studies find linear local-regional richness relationships, and the other ~50% find saturating ones.” Sorry, but Gonçalves-Souza et al. were way ahead of you on that–and it’s a non-starter. They looked at a whole boatload of ecological and methodological covariates: taxonomic group, trophic position, thermoregulation, adult dispersal mode, biogeographic realm, hemisphere, study design, and study scale. They found precisely nothing–none of these covariates explains why some studies find linear local-regional richness relationships while others find saturating ones. As far as we can tell, whether you see a linear or saturating local-regional richness relationship is a coin flip.
I think there are several lessons here.
First, there’s no longer any reason to study local-regional richness relationships. If that seems like an overly-strong conclusion to you, well, let’s review the bidding. Theory says that there all sorts of different processes or combinations of processes that can lead to linear local-regional richness relationships, and that those very same processes or combinations of processes also can lead to saturating relationships, depending on parameter values. So theory basically says “Anything can happen, it depends on a whole bunch of idiosyncratic and system-specific details.” And when we go out in nature and collect data, the results we obtain are almost literally a coin flip, the outcome of which can’t be predicted by any obvious predictor variable. Does this sound to you like a good starting point for further research? The data are a bunch of coin flips, the outcome of which we’re unable to predict, and theory says there’s no reason to expect anything else. Even if you admit that local-regional richness relationships aren’t a shortcut to mechanistic insight, and you just want to study and explain them for their own sake, why would you want to? With all the other actual patterns in the world that you could be studying? And what gives you any reason to think that you’ll be able to make any progress? As I’ve noted before, “Not much is known about X” is actually a reason not to study X!
Second, while I’m not so foolish as to think that the local-regional richness zombie actually has been slain (I’ve learned my lesson on that), I do wonder if Gonçalves-Souza et al. have at least dealt it a body blow. I say that because previous attacks on the local-regional richness relationship were different in character. For instance, mathematical theory is always going to have an uphill battle against people’s pre-theoretical intuitions. And technical issues like defining the boundaries of localities and regions are universal. Those technical issues really are the sorts of issues that need to be recognized, but that shouldn’t be allowed to halt a promising research program. But now Gonçalves-Souza et al. have shown that the existing data do not show what everyone thinks they show, even at a purely descriptive level. Similarly, in economics Paul Krugman wonders if the exposure of clear-cut empirical problems with the claims of Reinhart-Rogoff will undermine the influence of that paper in a way that conceptual and technical criticisms never could (see here for my discussion of Reinhart-Rogoff and its relevance to ecology).***
Third, if you say that, well, local-regional richness relationships were a dead end, but at least they spawned a lot of useful work, I respectfully disagree. Being influential doesn’t compensate for being wrong. Without meaning to be snarky at all or to put down anyone who’s worked on this (all sorts of great ecologists have worked on local-regional richness relationships), I think the following is a fair summary of what we’ve learned: “The local-regional richness relationship is linear about half the time, and saturating about half the time, a fact we can’t explain and from which we can infer nothing.” Going down blind alleys is unavoidable, and there is no shame in it (if we knew what we were going to find, it wouldn’t be research, as the saying goes). Again: this is a blind alley I myself went down at one point! But it’s nothing but unfortunate when we do go down a blind alley. Plus, as noted above, really serious criticisms of local-regional richness relationships as a shortcut to mechanistic insight have been published repeatedly since the late 1990s, and have been repeatedly acknowledged but never resolved. When first proposed as a shortcut, local-regional richness relationships were well worth pursuing. But I think the “shortcut” could’ve been recognized earlier for the blind alley it unfortunately turned out to be. I suspect Brian may disagree with me on this one, as in general he’s a strong advocate for “muddling through” with imperfect approaches in the hopes the future researchers will improve them. But in this specific case, few improvements have been forthcoming, and the methodological advances that we’ve made (such as logratio regression) often have been such as to reinforce rather than solve earlier concerns.
Fourth, I hope nobody tries to argue that we’ve just got to keep on keepin’ on with this research program, somehow building on what’s been done so far rather than just abandoning it, on the grounds that no alternative is available. Because there are plenty of alternatives! In particular, we’ve never been short on ways to test how open local communities are to colonization by species not currently present. Like, say, actually doing experiments to see if local communities are open to colonization by species not currently present. Those experiments aren’t even that difficult in many systems, which is why many such experiments have been done (think of seed sowing experiments to test the invasibility of plant communities, or the classic work of Jon Shurin in zooplankton communities). Similarly, if you want to know if the species within local communities are competing, and how strongly, you can do what a bazillion community ecologists have done and do straightforward removal experiments to find out. I’ve never understood the attraction of local-regional richness relationships as a shortcut to insight about the determinants of local species richness or the strength of local species interactions. In many systems, it’s straightforward to answer those questions via direct experimentation, so why do we need a shortcut here? Why approach those questions via a roundabout, highly-dubious inference from the shape of the local-regional richness relationship? (And don’t say, “Because we need to know if those local processes matter at larger scales”, because what happens at larger scales is just the aggregate outcome of what happens at smaller scales. I’ve discussed this more than once.) More broadly, there are all sorts of ways to study “metacommunities”, or the consequences of community “openness”, or the interplay of processes operating at different spatial scales, or etc. If we just give up on local-regional richness relationships, full stop, we are not going to be short on questions to ask about spatial community ecology, or perfectly-feasible ways of answering those questions! We really can just quit studying local-regional richness relationships without doing any harm to our ability to address any substantive question in ecology.
Local-regional richness relationships were a good idea at the time. Like many good ideas in science, it didn’t pan out. I think we could’ve recognized that earlier, but hey, whatever–the important thing is that we recognize it now. Time to admit that local-regional richness relationships were a dead end, rather than letting this now thoroughly-discredited idea persist as a zombie.
*Full disclosure: I reviewed this paper for Oikos. I’ve been planning to blog about it since I reviewed it, even though I don’t usually blog about new papers, because I think it’s a particularly important paper. But I decided to wait to post until the authors had their own post up on Oikos Blog, because I didn’t want to steal their thunder.
**Anyone else besides me wonder how much of the appeal of local-regional richness relationships as a shortcut is down to the fact that one can use the same word (“saturating” and variations thereon) to both describe a regression that reaches an asymptote, and to describe the ecological processes that putatively give rise to such regressions? This verbal fact has the unfortunate consequence of suggesting that the interpretation of the regression is almost inherent in the regression–almost as if no interpretation at all is required. And indeed, I have occasionally reviewed papers that mix these two things up, talking as if a saturating regression is one and the same thing as local communities that are saturated with species. Choice of words can mislead us in science, and I suspect it has done so in the case of local-regional richness relationships.
***To be clear, I am not saying that conventional analyses of local-regional richness relationships were goofs like Reinhart-Rogoff’s Excel blunder! All I’m saying is that the work of Gonçalves-Souza et al. pushes back against the conventional wisdom about local-regional richness relationships in a different, more empirical way than previous pushback.
Szava-Kovats et al. just published basically the same results in Ecology, two days before that Oikos paper: http://www.esajournals.org/doi/abs/10.1890/13-0244.1
Yes, I reviewed that paper too. I wrote the post about Gonçalves-Souza et al. because it was actually accepted before Szava-Kovats et al. was submitted, and because I knew Gonçalves-Souza et al. had come out. I hadn’t realized that Szava-Kovats was online now too. That it came out first indicates that Ecology and Oikos process mss at different rates after acceptance. I will update the post to give Szava-Kovats a shout-out as well. As you say, they reached the same results. The important thing here is not the priority, it’s that two groups working independently arrived at the same conclusions, both of which undermine the conventional wisdom on local-regional richness relationships.
Note that it’s not a given that two groups independently reviewing the same literature will reach exactly the same answer. Back in 1983 Tom Schoener and Joe Connell both reviewed field experiments on competition and famously came to somewhat contrasting conclusions.
I am thinking hard about your statement “because what happens at larger scales is just the aggregate outcome of what happens at smaller scales.” I haven”t read your linked texts, but anyway, this is a very broad-sweeping claim. Can’t local scales be shaped by e.g. facilitation and regional scales by e.g. drought? Of course this would still mean that the regional scale is the sum of local scales, hence the “aggregate outcome”, but if regions differ strongly in drought intensity that would be the primary driver at those scales, and not facilitation. I have no opinion on the local-regional richness relationship by the way, and your argument is plausible. Just my two cents here….keep up the good work!
The linked posts elaborate on what I mean, so I encourage you to click through. But you’ve got the right idea when you say “this would still mean that the regional scale is the sum of the local scales”.
I will give it a read, interesting. My comments stem from the fact that I study “the small(microbes)” (like you, as far as I know), so I don’t mind to claim “small scale processes rule the world”! 🙂
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Hi, I was just arrived at your blog this year and regretted that I did not find it earlier. I am a master student seeking for research question for my thesis and I was interested on the local-regional species richness pattern to somehow giving more stories to a bunch of of quick biodiversity assessments in my understudied country.
The problem with this zombie is that although intuitively I find it weird (local species pool will never exceed regional ones! Srivastava (1999) clearly said the weirdness of the methods available and arbitrary null-model), but there are a large body of literature studying it anyways so I was thinking that I might missed something and keep researching literature in the topic until I find the Szava-Kovats et al (2012) and Gonçalves-Souza et al (2013) paper, and then your blog post when I googled “how to make local-regional species richness plot”. Now I am lost, hahaha.
I am looking to their conclusions and recommendations and I find that reciprocal relationship is still worth it to investigate (?) more like process-oriented rather than just pattern. Or just adding an empirical evidence of the pattern using the methods of their paper?
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Thanks for the post. Belatedly finding it now. Couldn’t agree more. Am only waiting for any examples of negative slope to totally throw us. Otherwise any form of positive slope just doesn’t contain much information.
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