Guest post by Carsten Dormann (Uni Freiburg) / @CarstenDormann
The relationship between species richness and ecosystem function is a field of ecology that has always puzzled me. I learned the scientific rope in a department of vegetation ecologists: vegetation was the result of environmental conditions, and indeed a substantial part of their research was to quantify what a plant species indicates about its environment (think Ellenberg indicator values). While of course species may be absent from a community due to competition, those species that are there reflect climate, soil, management.
Thus, when I see a paper showing a strong effect of species richness, I feel that there must be something amiss. (This paranoid and blanket scepticism goes far beyond “biodiversity” effects.) Can it really be true that in a give-or-take “natural” system we can boost productivity by 100-200% by having more species? Looking out of my office window, I can make out the Black Forest, and a nice large monoculture of spruce. Will adding a random local tree species increase the productivity? And does a mixture of, say, beech and spruce with a higher productivity demonstrate a TSR effect on P?
Actually, this blog post is an appetizer for our re-analysis of Liang et al. (2016, Science). But bear with me for another brief excursion. Let me first repeat an argument I read in Donald Maier’s scathing critique of “biodiversity research” (Maier 2012: “What’s So Good About Biodiversity?”, Springer): When we plot species richness on the x-axis, we assume that the species we count are equivalent. If they weren’t, their number is not helpful, and we should quantify something else, e.g. a trait or their abundance or their composition; but not their number. And, when investigating the effect of TSR, the x-axis implies random species composition. If it wasn’t random, then richness would be confounded with something else. (Admittedly Maier put it better, but also more verbose.)
Liang et al. (2017, Science: “Positive biodiversity-productivity relationship predominant in global forest”) present such a figure, with an increase in productivity on from around 3.5 to well over 10 m3ha-1yr-1, as “relative species richness” increases from little to 100% on the x-axis. Such a figure rings my alarm bells. So, together with two BSc students, we re-analysed the data presented in that paper.
There are various points that we consider problematic (be it extremely unrealistic values for P; Euclidean distances between plots on a spherical world; non-stratified sampling of biomes; computation of “bootstrapped” error bars), and we investigated them one by one, but the pivotal point is the x-axis: What does “relative species richness” mean? Quite simply, it is the number of tree species in a plot divided by 270, the highest species richness in the data set considered. (Now that is a tiny bit unfair, but it is essentially what it is. In the rundown of the re-analysis we of course use Liang et al.’s definition.) So, a 10-species plot in Finnland receives a value of 3%, while a plot in Panama gets a value of 100%. Can you spot the problem? Yes: the TSR gradient is in fact a latitudinal gradient. That, in turn, means that the plot does not depict the effect of TSR on P, but of latitude on P!
We were still charmed by the idea of constructing an x-axis that is relative. Instead of “relative to the highest richness in the tropics”, however, we constructed a tree-species richness relative to the highest number of tree species observed in that region. So 100% means “as many as you can get around here”, and varies between 5 tree species in Siberia and 500 in Panama.
Using this definition (and stratifying by biome, and correcting for spatial distances on a sphere, and using subsampling correction for error bars) we find — nothing. (A tincy effect to the eye indistinguishable from a horizontal line.)
Diversity-productivity relationships where diversity is either defined relative to the global maximum (beige) or the local maximum (green)
Of course, when looking at each biome separately, we find more or less positive effects, but never as strong as in the original global analysis.
Interested? Read more in our preprint on bioRxiv here!
What to take home? Well, perhaps that observational data are tricky for estimating richness effects. It’s so easy to miss effects and then wrongly attribute changes in productivity to species richness (And yes, I include Duffy et al.’s meta-analysis 2017 in this criticism; it’s part of my paranoid scepticism).
theoretical ecology 
Hi Carsten,
reading through this, I had a general comment, and a question.
The general comment is about your introductory remarks, which one could interpret, in some sense, as explaining your prior on the strength of BEF effects, based on your “scientific upbringing”, common sense, and your reading of the literature. If I summarise your remarks correctly, you say that you see neither good theoretical, nor empirical support for (strong) BEF effects.
I guess I kind of agree with the empirical side of this (particularly for forests, BEF effects seem to be small), but I would point out that from our ecological theory, it’s not crazy to expect BEF effects in RANDOM assemblies (via functional complementarity etc). What I find being glossed over too often in these discussions, however, is that complementarity can only play out if you have a pool of functionally complementary species that are nevertheless competitive in the given environmental conditions (if not, you have selection effects, which create a trivial effect in experimental BEF studies, and no BEF effect at all in observational studies). It seems to me that temperate tree species are simply not numerous enough (particularly in Europe) that the environmental niche space could be densely packed, which is why I would expect that selection effects often overpower complementarity effects. A further question is what options trees have to diversity functionally, apart from their climatic adaptation. In general, however, I guess I come to a similar conclusion, but with a different reasoning (i.e. that I could imagine strong BEF effects in theory, but not temperate trees).
My question is the following: your conclusion that the pattern in Liang et al. 2016 is mainly explained by climate makes total sense to me, but the paper did (try) to control for climate (when I understand their eq. 1 correctly). Moreover, the authors are obviously aware of the problem, as they state it in the paper
“We focused on the effect of biodiversity on ecosystem productivity. Recent studies on the opposite causal direction [productivity-biodiversity relationship (14, 36, 37)] suggest that there may be a potential two-way causality between biodiversity and productivity. It is admittedly difficult to use correlative data to detect and attribute causal effects. Fortunately, substantial progress has been made to tease the BPR causal relationship from other potentially confounding environmental variables (14, 38, 39), and this study made considerable efforts to account for these otherwise potentially confounding environmental covariates in assessing likely causal effects of biodiversity on productivity.” (Liang et al. 2016)
I think that “there may be a potential two-way causality between biodiversity and productivity” is a mild understatement, given that the LDG (which usually has the arrow in the different direction) is probably the most iconic macroecological pattern of our entire field. Moreover, as we point out in our recent review on the LDG (Pontarp et al., 2019, TREE), there is not only the hypothesis of productivity influencing diversity, but also many other factors that are collinear with latitude (e.g. climatic stability) and that could therefore act as statistical confounders in a static analysis.
With that being said as background, my question is
1. If we would take the strong prior (based on our ecological understanding) that the latitudinal pattern in productivity is caused by climate and not diversity is just spuriously correlated aside and imagined we knew nothing about ecology, is there a reason to prefer your statistical analysis over Liang et al. 2016?
2. Do you have any intuition why their control for climate failed so spectacularly to conform with ecological understanding? I guess it may simply be impossible to separate the arrow of causality in this type of analysis?
In general, I guess one could summarise this as asking: is this really a statistical question, or does it boil down to our prior about the arrow of causality?
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Hi Florian.
I think you open several cans of worms in your comment. Can I choose which to have an opinion on?
1) Is this a statistical question?
No, I think it is not. The authors had an idea behind computing “relative species richness” the way they did. I’m reading between the lines here, but I think they thought that each species has some niche space (volume, rather), and that more species fill more volume. Hence, “relative species richness” is a measure of niche volume filled. That reasoning also peeks through in your comment: “temperate tree species are simply not numerous enough … that the environmental niche space could be densely packed”. — I disagree. My “feeling” (or “subjective ecological comprehension”) is that niche space is dramatically smaller in colder climates (for trees). Being able to survive freezing for months, high temperatures in winter, browsing by ungulates: there are so many constraints on the life history of a tree in temparate forests that we are left with a tiny realisable niche space: enough for the 20-50 tree species we observe. Thus, I find it ecologically wrong to divided by 271, because that (to me, implicitly) assumes that niche volume is the same in the tropics and the boreal. Our analysis (dividing by local species richness) is not particularly convincing either, I agree. It is IMHO better, but not good (because realised S is not necessarily a good proxy for niche volume). Indeed, I much prefer the analysis with species richness itself on the x-axis: it quantifies the realised complementarity with each new species, and that is interesting.
2) Why did the control for climate in Liang et al. not suffice to “reign in” the richness effect?
Well, firstly because their richness is weird (see previous point).
Secondly, they use a linear, strictly additive model for climate effects; maybe a bit more flexibility would help. (Actually, I use the interaction of rain and temperature as OBVIOUS example to introduce statistical interactions in the BSc statistics lecture. Higher temperatures will only increase productivity when matched by higher rainfall. Otherwise the deserts would be full of trees. Why Liang et al. did not find that an obvious interaction to add, and whether it would have made a difference, I don’t know.) You are welcome to the data and my preparational code to try yourself to improve their model and get a better fit for the climate and soil.
Thirdly, I very much like the paper of Díaz et al. (2007, PNAS), where they set up a whole chain of preconditions to be checked before attributing something to “species richness” itself. Liang et al. have not done that (largely because the required trait data are not available for most plots).
3) What do you mean by “diversity”?
No, I’m not regurgitating the entire sampling effect debate and alike. I only want to point out that, as a famous diversity researcher said in confidence: “We don’t interpret species richness on the x-axis as species richness. Rather, it is a proxy for functional diversity.” Sure, if that is how you see it, I do expect substantial diversity effects. But what we re-analysed were species richness, not something else. And this possibly silly measure “species richness” was not particularly helpful to explain productivity in that data set.
So, in a nutshell: I expect huge effects of environment on species richness, and on productivity. I expect substantial effects of biomass on richness (through competition). And I expect small effects of “species richness per se” on productivity or biomass. It certainly is bidirectionally causal, with a hefty arrow in one, and a barely visible one in the other direction. (Ooops, seems I didn’t learn anything since my Master degree.)
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Hi Carsten,
re 1): yeah, maybe. I guess regardless of the niche space discussion, the main point is probably that it’s reasonable to assume that the global LDG is CAUSED by other things (no agreement on which), and that there is a trivial latitudinal gradient in productivity, so a large part of the naive global correlation of prod ~ div is probably spurious.
re 2): OK, fair enough. I suspect in any case that our prior on 1) is probably the crucial determinant of what we’ll get out of this analysis.
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Hi Carsten, could you comment on your criticism/scepticism regarding Duffy et al.’s meta-analysis?
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Hi Thomas.
I hesitate to comment on the Duffy et al. paper, because I have not devoted nearly as much time to it as to the Liang et al. I did download their supplementary material to see how many environmental predictors they had in their model … Ah, hang on: First an introductory sentence for the interested reader.
Duffy et al. meta-analyse studies that correlate ecosystem function (say productivity, P) with species richness, S. Obviously both may be driven by a common factor (such as climate), and hence the P ~ S-relationship needs to be corrected for such confounders. Duffy et al. did not do that themselves, but trusted the original papers to having successfully removed ALL environmental or management effects on P, so that their regressions for the effect of S is in fact SOLELY due to species richness.
(Back to before the background sentences:) On average, the studies corrected for 2 and a bit preditors (mainly climate). I find it, well, naive to believe that with 2 predictors you encapsulate ALL environmental effects FULLY. If you don’t, you overestimate the effect of S. That is what I believe happened in their analysis: They incorrectly attribute environmental effects to species richness, simply because the original authors did not include enough/the right predictors.
To be honest, I can’t tell. Every individual study must be re-analysed to tell, adding management, soil, climatic extremes (rather than averages), species identity effects, community-weighted mean effects, etc (sensu Diaz et al. 2007 PNAS), possibly even adding spatial effects uncorrelated with S, and only then I might tentatively consider the remaining S-effect to be valid. As far as I can tell, none of the meta-analysed studies did that. I thus consider all of them to be inadequate for demonstrating a species richness effect. Hence, also the meta-analysis cannot.
I hope that Duffy et al. (or their friends) don’t read this reply! I am still bruised by months of interacting with Liang et al., and I am not ready to take on another “fight” just yet. So, this is just between you and me 😉
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Thanks for overcoming your hesitations 😉
I guess part of a reply to your concerns lies in the argument that they included the main drivers of productivity and that the positive richness-productivity (or richness-biomass) relationship typically got even stronger when correcting for the confounding variables.
Anyways, I definitely agree that it’s almost impossible to consider ALL environmental effects when comparing different locations. That is why I would say that in cases when there is a positive relation (as e.g. in 5 of the 11 ecoregions for your re-analysis), species richness can serve as useful indicator for function (same for other suitable measures of (functional) diversity; many are better than richness per se, but the issue of confounding environmental factors should in principle apply to all). Moreover, although biodiversity is not the sole driver of functions, I agree with Florian and you that complementarity effects make sense. They may also operate in real communities. So biodiversity may be one (important) driver of functions. Certainly, disentangling the causes for differences in functions, and potentially separating “direct effects” of environmental factors on function from “indirect effects” via altered community composition, can be attempted more often in future.
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Some useful points here, thanks. We also had some concerns on this study which we have finally published here https://rdcu.be/b028p (open access, n.b. we point readers to your BioRxiv piece too)
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