The Ghost of Plasticity Past, or Why Plasticity Inferences are too Plastic

Several months ago, I attended a meeting of the American Genetics Association organized by Robin Waples in Seattle, Washington. The theme for the meeting was “Evolution and Plasticity: Adaptive Responses by Species to Human-Mediated Changes to their Ecosystems.” The meeting was a particularly clear example to the current excitement about the role of plasticity (including epigenetics) in the evolutionary process – an enthusiasm that really crystalized around Mary Jane West-Eberhard’s “Developmental Plasticity and Evolution”. Much of the excitement centers around the idea that plasticity (a single genotype has different phenotypes in different environments) can promote evolutionary change. For instance, plasticity can provide the raw material necessary for evolutionary change by revealing otherwise cryptic variation. In addition, plasticity might generate immediate adaptive phenotypic shifts that allow individuals and populations to persist in new environments, thus allowing and promoting subsequent adaptation (without the initial adaptive plastic shift, the population would have gone extinct). This idea is not new, having originated with James Baldwin in 1896, but it has certainly become vastly more popular of late.

These (and other) ideas for how plasticity might promote evolution are certainly interesting, but how does one go about testing them? One of the things I found simultaneously most interesting and frustrating about the Seattle meeting was that seemingly any pattern in the data was being interpreted as evidence that plasticity promotes evolution. Perhaps most commonly, a finding that plastic responses to a particular environmental difference were in the same direction as evolved differences between populations evolving under the same environmental difference was interpreted as evidence that plasticity promoted evolution. For instance, guppies might shoal more in the laboratory when exposed to predator cues and guppy populations evolving with predators might shoal more than those evolving without predators (independent of proximate predator cues in the laboratory). On the exact opposite hand, however, evidence that plastic responses to a particular environmental condition were in the opposite direction as evolved differences was also interpreted (by other presenters) as evidence that plasticity promoted evolution. In this case, the idea is that the plasticity is likely maladaptive and so requires evolutionary compensation.

The current inferential scheme for whether or not plasticity promotes evolution

If either of two opposite patterns is interpreted as evidence for the same thing (i.e., plasticity promotes evolution, albeit in different ways), how do we proceed with rigorous hypothesis testing. Surely we also need a set of results that would be interpreted as evidence that plasticity does NOT promote evolution. That is, the hypothesis must also be clearly falsifiable through some particular outcome in the data. The lack of such a criterion reminds me of the classic criticism by Joseph Connell that competition was invoked when species have similar diets (because they obviously then use the same resources) and also when species have different diets (because past competition had presumably reduced diet overlap – the ghost of competition past).

In the past, when I pointed out to some ecologists that competition seemed of little importance as a mechanism determining a particular species' distribution, they often gave the following answer. The reason, they said, for my inability to find evidence for competition was because it had already been eliminated by past coevolutionary divergence between those species. However, for the reasons discussed in this paper, and until some strong evidence is obtained from field experiments along the lines suggested above, I will no longer be persuaded by such invoking of "the Ghost of Competition Past". (Connell 1980 – Oikos)

Although the Seattle meeting ended several months ago, I was just prompted to write a post about the topic owing to the recent publication in Nature of another study about the role of plasticity in evolution: “Developmental Plasticity and the Origin of Tetrapods.” Em Standen, Trina Du, and Hans Larsson wanted to test whether plasticity would promote major evolutionary transitions, especially the transition from swimming in water to walking on land. To test this possibility, they invoked a classic hypothesis test: if an ancestral species shows adaptive plasticity in response to an environmental shift, and that plasticity mirrors the evolutionary changes that accompanied the environmental shift, then plasticity likely promoted the transition. Specifically, they reasoned that rearing an air-breathing fish out of the water (by misting them regularly) would cause developmental changes in morphology that would lead those fish to be better walkers out of water. If so, the same thing may have taken place in the water-to-land transition. This is a cool idea – although, of course, plasticity in the ancestor is merely consistent with the hypothesis rather than proof of it.

The difficulty in any such study is that the actual ancestor (here the ancestor of land-dwelling tetrapods) is not accessible for study – and so Standen and colleagues needed an analog species. Coecocanths obviously wouldn’t work and lungfish are just too pathetic on land. So the authors chose to use another basal tetrapod – the Polypterus or “bichir.” Performing the experiment, they found that Polypterus raised out of water were indeed better at walking out of water than those raised in the water (see the cool video below) and showed developmental morphological changes that were similar to those in the fossil record associated with the move out of water.

This result is fascinating and I was privileged to see its implementation as the work was done in the lab of my close colleague Hans Larsson. In fact, I was able to talk to him about it multiple times on the train on the way to work. In addition to simply be jealous that I hadn’t thought of it first, I came to crystallize a particular criticism of the work. Specifically, I contend (if only as Devil’s Advocate) that the results could just as easily be interpreted as showing that developmental plasticity does NOT promote evolution. The reason is that Polypertus has never made the transition to land despite millions of years of opportunity to do so. Thus, all this wonderful plasticity did NOT accomplish the task it is inferred to assist.

Given all these flexibility in ad hoc interpretation, it seems to me that the field needs a critique and a careful (a la Connell) outline of the various patterns that might be observed in an experiment and what inferences they would and would not allow. Until such an endeavor is undertaken and adopted, inferences about plasticity are simply too plastic.

I wrote the above on the train a few seats away from Hans and, while then walking to work, we discussed what the optimal experiments would look like. We think that the ideal approach would be experimental evolution: have replicate plastic and non-plastic genotypes/populations, expose them to new conditions, and track their subsequent evolutionary trajectories. If the most plastic genotypes show the fastest and most dramatic evolution, then plasticity promotes evolution. If the least plastic genotypes show the fastest and most dramatic evolution, plasticity constrains evolution. If plastic and non-plastic genotypes don’t differ, plasticity does not influence evolution. Until then, I will no longer be persuaded by such invoking of "the Ghost of Plasticity Past".