Why my money is still on transitivity in plant communities

Guest post by Carsten F. Dormann

In his book “The Signal and the Noise”, Nate Silvers likened competing scientific hypotheses to betting. If you think that your hypothesis H1 is correct, rather than H2, you should be willing to put money on it, with odds reflecting your belief in H1 vs H2. This post collects a few thoughts on the claim that “Intransitive competition is widespread in plant communities and maintains their species richness” (Soliveres et al, 2015, Ecology Letters), and explains why my money is still on transitive competition in plant communities.

What is transitivity?

Transitivity of competition refers to the order of dominance between species. If we know that A is dominant over B, and that B is dominant over C, then transitivity means that A should be also be dominant over C. In short form: If A > B and B > C, then A > C. The opposite case, in which C > A, is called intransitivity of competition.

carstentransitivitycomment2

An illustration of a intransitive relationship between species A,B,C

In my own little experimental contribution (Dormann, C.F., 2007), my reading of experimental studies in plant communities was that no evidence existed for a single case of intransitivity: in all experimental cases, dominance was “handed down”. As I didn’t follow the literature on this subject closely, my “belief” today is formed by what I knew then. I was therefore struck by the title of the paper by Soliveres et al. (for sake of simplicity let’s call it SEL, for Soliveres in Ecology Letters). Before reading the article, my Bayesian prior was pitched highly against it; and it would have taken substantial evidence to overturn my belief. The paper did not manage to do that, not one bit, and I want to explain why:

Why Soliveres et al. does not change my prior on transitivity

The study of SEL reports on an analysis of abundance data for plant species from two separate research consortia. The authors use an approach proposed in 2014 by Ulrich et al., where the observed site-by-species matrix is deconstructed into a “competition matrix” C (representing pairwise competition effects) by means of a transition matrix P. The degree of transitivity, tC, is computed from C. There are a few preparational steps in the SEL analysis, which I will not address further, because I don’t see that they affect any argument below. Here is the number list of reasons, why I think that this analysis cannot reveal (in)transitivity and hence update my prior belief:

1. The process-from-pattern problem

The data at hand are observed plant community compositions in many sites (which the authors cluster together in order to make them homogeneous per cluster). Composition will certainly have a large variety of causes, including soil properties, land management, competition, fungal infections, nematode grazing and so forth. The authors’ approach assumes competition as main drivers of the pattern. That SEL finds good fits of their model to the data shows “only” that indeed intransitive competition could produced a pattern consistent with observations. No alternative processes were tested or explored, so we have no way of telling whether SEL’s competition-only assumption fares better than, say, a management-only, or a soil-by-nematodes or any other process may underlie the observed pattern.

More general, it is notoriously difficult, and probably often impossible, to infer processes from observational patterns. If, for some reason, we had a very strong mechanistic basis for a prediction, then observations may fail to reject this prediction, and the underlying theory. What SEL claim, however, is that they detected intransitivity, and that it explains the observed pattern. In the absence of alternative hypotheses tested, the strongest statement they could make, philosophically, is that the observed ‘pattern is consistent with intransitive competition. That is a far cry from the actual claim.

2. No new experimental or theoretical evidence to alter my prior

In the introduction and discussion, SEL run through the most relevant papers for their theory. I (re)read those I didn’t know, hoping that there are some that shift my prior disbelief in intransitivity. What I found instead was a logical flaw (as I see it) in the reasoning of SEL. They cite several studies that show that intransitivity can yield coexistence in competitive communities (Gilpin 1975, Huisman et al. 2001, Allesina & Levine 2011). Let me state that again: If communities are purely competition-structured, then intransitivity allows for coexistence. I agree. But this is largely irrelevant to the claim of detecting intransitivity, for we cannot assume that plant communities are purely competition-structured. Thus, there is a circularity in the argument: SEL assume competition, which allows them to use a competition-only method, which detects intransitivity, which confirms that competition structures plant communities, which “confirms” their assumption.

SEL also acknowledge that intransitive hierarchies have been found only in non-plant organisms (bacteria, lizards and bryozoa). They cite another observational study as demonstrating the importance of intransitivity (Freckleton et al. 2000), which not only doesn’t ever discuss transitivity, but also does not provide any data from which I can deduce intransitivity (indeed, the three species investigated there all show competitive effects onto the other species, but I see no inversion of the Lolium > Vulpia > Trifolium hierarchy). In contrast, the cited study of Grace et al. (1993) failed to detect any intransitivity for six species in three different years. It seems to be a straw man to claim several times “the absence of a competitive hierarchy” without a single plant community reference in support, but ignore the (few) studies that demonstrate hierarchies (incl. Keddy’s reasonings on the subject: Shipley & Keddy 1989, Keddy & Wisheu 1992, Keddy et al. 1994, Keddy 2001). This tricks the reader into a “flat prior”, while the evidence IMHO is strongly rejecting intransitivity in plant communities.

Thus, I found no new experimental evidence to shift my prior belief in transitivity in plant communities.

3. This specific method cannot discriminate competition from other effects.

(This point is probably my weakest, as I have not used the approach myself, and thus have no hands-on experience with it.) The competition matrix C parameterised by the approach of Ulrich et al. (2014) represents net effects of all processes in that community. By restricting its application to plots “as homogeneous as possible” (SEL p. 792; homogeneous in environment, or in composition?), the hope is that it is mainly competition that is picked up. But why should that be? And what is the evidence that it is: neither Ulrich et al. (2014) nor SEL simulate non-competition communities to demonstrate that only the competition signal is represented in C. And, no matter how homogeneous, all other processes of community ecology still act: invertebrate herbivory, fungal infections, selective livestock grazing, etc., many of which can look like competition (hence Holt’s 1977 phrase of “apparent competition”), and arguably can be described by competition models, but are very different processes. If the authors were to acknowledge that their “competition” matrix C is a hotchpotch of all these processes, I had no objections, but it would kill the title statement.

Interestingly, the intransitivity metric (I = 1 – tC) was positively correlated with spatial segregation of plants in plots (rho =0.59). As spatial segregation is a way to reduce interspecific relative to intraspecific competition, I may actually be a useful index of net coexistence effects. Since segregation can have various causes (e.g. dispersal limitation, soil microsites), it cannot be solely attributed to competition.

In summary: So far, all experimental studies in plant communities have demonstrated that competition is transitive. What that means is that everyone in the field of plant community ecology should have held my prior belief, including the authors, and given that, that we should apply Laplace’s weight of argument (“Plus un fait est extraordinaire, plus il a besoin d’être appuyé de fortes preuves”, or in English: “The weight of evidence for an extraordinary claim must be proportioned to its strangeness.”). Observational studies cannot provide strong evidence for a process, particularly not if only one candidate mechanism is investigated. It is thus unlikely that an observational study can trump collective experimental evidence, and that the claim of the paper’s title can be upheld.

Towards a resolution

In the Gilpin paper, I found an interesting quote, which gave me a lead on why SEL and I have different opinions. It is from an obscure book chapter by Richard Lewontin (of population genetical fame): “A great deal is made of transitivity. If I prefer A to B and B to C, then rationally I will prefer A to C. But biological systems do not always behave this way, alas; there are significant departures. It is possible to show experimentally that if, in a competition situation, genotype A eliminates genotype B, and in another situation genotype B eliminates C, it does not follow at all that A will eliminate C in direct competition. On the contrary, there may be unique interactions that reverse this.”

The two key ideas here are “in another situation”, and “interactions that reverse this”. I interpret this as saying that under different environmental or biotic conditions, competition hierarchies may be inverted (giving rise to across-site intransitivity). Could it be that SEL and I simply compare different set-ups? My interest is in the question “Given a plant community under some constant condition: will there be any intransitivity?” And I believe the answer still is: no. But re-reading the text in SEL, I get the impression they ask: “In plant communities of a comparable type, are there intransivities?” They compare communities in different environments, where soil structure, management, pollinators, insect herbivores, microclimate and many other things change. If that is their question, I fully agree with their conclusion: Yes, as the environment changes, so will competitive effects, and possibly even the competitive order. (Although why fertilisation should increase rather than decrease intransitivity, as claimed on page 791, is unclear to me.) I do not like the idea of calling this a competition intransitivity, however, as succession, storage effect and most other stabilising mechanisms would be subsumed. Intransitivity in that respect is a step back from a mechanistic understanding of community processes, not a step forward.

Allowing for these different perspectives solves the discrepancy between finding intransitivity or not: yes, across sites; no, within sites. SEL and I are now happily married – or are we? Well, the title has a second part: “and maintains their species richness”. It seems bizarr to refer to a process that maintains species richness across sites “intransitivity”. I therefore must interpret SEL as proposing intransitivity within sites to maintain species richness. This view is supported by their cited literature on intransitivity, which looks at only one community. Now, I have to disagree again: I see no evidence for within-site intransitivity, and hence cannot accept the claim that this maintains species richness. The mechanism that SEL attribute to “competition intransitivity” by now has dissolved into something quite different: stabilising coexistence in fluctuating environments, e.g. through the storage effect, non-linearity of competition, or indirect interactions (see Chesson 2000). My understanding is thus that the “transitivity index” τC may be a useful index of the net outcome of all sorts of processes at the community scale, and their net effect on coexistence. Keeping the name seems not indicated, however, as it would wrongly suggest that transitivity is the cause.

Conclusions

When any of the authors of the SEL paper and I meet, I guess I will have to put money where my mouth is and offer them a bet (in the spirit of Nate Silvers). What are the odds that they are right, and I am wrong (taking into account the many co-authors, good journal, peer-review, experience)? Well, my betting odds are 20:1 that competitive intransitivity does not exist in any relevant amount in local plant communities. The problem I foresee is to agree on how to decide who won when future evidence comes in, as we seem to have different working definitions of what competitive intransitivity means.

References

Allesina, S. & Levine, J.M. (2011) A competitive network theory of species diversity. Proceedings of the National Academy of Sciences of the United States of America, 108, 5638–5642.

Dormann, C.F. (2007) Competition hierarchy, transitivity and additivity: investigating the effect of fertilisation on plant–plant interactions using three common bryophytes. Plant Ecology, 191, 171–184.

Freckleton, R.P., Watkinson, A.R., Dowling, P.M. & Ley, A.R. (2000) Determinants of the abundance of invasive annual weeds: community structure and non-equilibrium dynamics. Proceedings of the Royal Society of London B, 267, 1153–1161.

Gilpin, M.E. (1975) Limit Cycles in Competition Communities. The American Naturalist, 109, 51–60.

Grace, J.B., Guntenspergen, G.R. & Keough, J. (1993) The Examination of a Competition Matrix for Transitivity and Intransitive Loops. Oikos, 68, 91–98.

Holt, R.D. (1977) Predation, apparent competition and the structure of prey communities. Theoretical Population Biology, 12, 197–229.

Huisman, J., Johansson, A.M., Folmer, E.O. & Weissing, F.J. (2001) Towards a solution to the paradox of the plankton: the importance of physiology and life history. Ecology Letters, 4, 408–411.

Keddy, P.A. (2001) Competition, 2nd edn. Springer, New York.

Keddy, P.A., Twolan-Strutt, L. & Wisheu, I.C. (1994) Competitive effect and response rankings in 20 wetland plants: are they consistent across three environments? Journal of Ecology, 82, 635–643.

Keddy, P.A. & Wisheu, I.C. (1992) Competition and centrifugal organization of plant communities: theory and tests. Journal of Vegetation Science, 3, 147–156.

Shipley, B. & Keddy, P.A. (1989) Competitive hierarchies in herbaceous plant communities. Oikos, 54, 234–241.

Soliveres, S., Maestre, F.T., Ulrich, W., Manning, P., Boch, S., Bowker, M.A., Prati, D., Delgado-Baquerizo, M., Quero, J.L., Schöning, I., Gallardo, A., Weisser, W., Müller, J., Socher, S.A., García-Gómez, M., Ochoa, V., Schulze, E.D., Fischer, M. & Allan, E. (2015) Intransitive competition is widespread in plant communities and maintains their species richness. Ecology Letters, 18, 790–798.

Ulrich, W., Soliveres, S., Kryszewski, W., Maestre, F.T. & Gotelli, N.J. (2014) Matrix models for quantifying competitive intransitivity from species abundance data. Oikos, 123, 1057-1070.

 

One thought on “Why my money is still on transitivity in plant communities

  1. I’m late to this post, but I think you put your finger on a really important issue – transitivity across constant conditions or transitivity across all conditions. The latter seems like a very tough thing to meet. But I agree with you that I think there is pretty good evidence for transitivity under constant conditions.

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