Some time ago, I wrote a post called “High Enthusiasm and Low R-Squared” in which I commented on how some research subjects seem to garner interest far greater than their real importance to ecology and evolution. One example I gave was genes of large effect, which are all the rage in scientific tabloids yet probably contribute to only a minor fraction of overall adaptation. Another example was biodiversity-ecosystem function relationships, which often have low explanatory power. That is, for a given biodiversity level, the range of ecosystem function is very large – even within a single experiment. A third example was parallel (or convergent) evolution, where instead most adaptation seems to be non-parallel (and non-convergent).
|From my forthcoming book "Eco-Evolutionary Dynamics"|
The fourth example I gave was so called “behavioral types” or “personalities” (and the related idea of behavioral “syndromes”), for which I argued that – in reality – behavior at any one time (or context) is usually not very predictive of behavior at another time or context. I didn’t mean to suggest that behavioral types weren’t interesting and, in fact, my former postdoc Lisa Jacquin just published in the Journal of Evolutionary Biology our cool study of how behavioral types evolve in Trinidadian guppies in response to different predation and parasitism regimes. (Although a reviewer made us excise most mentions of “personality” from the MS.) Rather, the point of my original post was simply that behavioral types might be overblown with regard how much research emphasis was placed on them.
|Bold versus shy for guppies from different predation and parasitism regimes - from Jacquin et al. (2016 - J Evol Biol).|
I am currently toward the end of a two-week trip to Europe that included stops in southern Switzerland, Zurich, Berlin, and Leuven (Belgium). After the first stop, which was for a conference/workshop on the “Genomic basis of eco-evolutionary dynamics,” I wrote a post that revised my original criticism of one of the above areas – genes of large effect. While I remain confident that most adaptation is the result of genes of small-to-modest effect, I am now also interested in the possibility that some specific genes might have reasonably large effects on eco-evolutionary dynamics. We might call them “keystone genes” in echo of Bob Paine’s keystone species idea. (Sadly Bob recently passed away.)
My second visit on the trip was to the IGB (Leibniz Institute of Freshwater Ecology and Inland Fisheries), where I was hosted by Robert Arlinghaus. A series of discussions on that visit have motivated me to revisit another of my suggested areas of “high enthusiasm and low r-squared.” A number of people at the IGB study behavioral types and some also examine the influence of those types on ecological processes. Yet- to expand my earlier criticism – behavioral types might not have much influence on ecological processes because behavior is quite variable to begin with (i.e., “types” are not really that consistent) and individual-level behavior might or might not have much influence on ecological function. To address these concerns we need to calculate the effect size of behavioral types, ideally in relation to how the same ecological parameter is influenced by some other causal force that we already know is important. So what we need is an experiment that asks about the effect size of behavioral types in relation to other drivers of ecological function – and why not “ecotypes”?
Ecotypes are, classically, populations adapted to particular environments, such as benthic versus limnetic feeding environments for fishes, different soil types for plants, high-predation versus low-predation environments, and so on. A lot of work on fish (whitefish, stickleback, guppies, alewives) has shown that these ecotypes differ in their influence on various community and ecosystem level ecological processes. So why not implement an experiment explicitly comparing the ecological influence of different ecotypes (e.g., fish obtained from populations adapted to different environments) to the ecological influence of different behavioral types (e.g., fish within those populations that are either bold or shy). Although this particular comparison would certainly be interesting, it is unfair in one respect. The “ecotype” effect is between populations, where evolutionary divergence is possible, whereas the behavioral type effect is within populations, where evolutionary divergence is more difficult.
|The ecological effects of some fish ecotypes - also from my book.|
Fortunately, we do have a “fair” and appropriate comparison to make. In addition to situations where benthic versus limnetic ecotypes are separate populations, such as in different lakes and sometimes even within lakes, many fish populations also show continuous quantitative variation among individuals along a continuum from limnetic to benthic. That is, within any given population in a given lake, some individuals will be specialized for limnetic feeding and others for benthic feeding. Using such a population, one could perform a mesocosm common “gardening” experiment crossing behavioral type (presumably assayed before the experiment) with ecotype (perhaps based on capture location – inshore versus offshore – or on characteristic morphology or coloration). One could then assess the relative importance of these two factors for the usual ecological parameters, such as zooplankton abundance, water clarity, DOC, benthic invertebrate communities, decomposition rates, and so on.
Beyond the just-noted benefit of allowing a direct comparison between the effects of behavioral type and ecotype, this experiment has another advantage – it can consider interactions between the two levels of variation. For instance, the effects of a given behavioral type (e.g., bold or shy) might be evident only for a particular ecotype, and so an experiment crossing the two levels of variation has the potential to increase one’s ability to detect the effects of either. Of course, the effect of a given behavioral type or ecotype on ecological variables likely also depends on the testing environment: bold versus shy might only matter for benthic fish in benthic environments. So one would ideally cross behavioral type with ecotype with testing environment in a fully crossed design. In addition, if one is to make general statements about the effects of ecotype or behavioral type, one would want to do the experiment for at least two independent populations – that is, testing the parallelism across evolutionary replicates of interactions between behavioral type, ecotype, and testing environment shaping ecological function. Yes, I realize this is a massive undertaking but I think we should at least consider the ideal experiment before then chopping it down to a more manageable subset.
Behavioral types and ecotypes might be correlated within populations (benthic fish might be more shy) and so separating the two effects might be difficult. Yet it remains critical. Imagine that behavioral types are closely correlated with ecotypes, such as when foraging environment or predator environment leads to the evolution of different behavior types – or vice versa. In such cases, an experiment focusing on only one or the other axis of variation would be unable to determine the true causality – because the two axes (behavioral type and ecotype) are closely correlated. That is, the apparent differences in ecological effects between two behavioral types might arise simply because behavioral type is correlated with (other) aspects of ecotype – and those other aspects are what drives the ecological effects. In this case, behavioral type is not the causal factor despite appearing so in the experiment. Thus, it seems most profitable to first examine the association between behavioral type and ecotype (within and among populations) and then – through careful selection of individuals that break the mold – that is, that cross the two factors to the extent possible.
I hope that this post will inspire someone toward such an experiment. If behavioral types prove to be as important as ecotypes for eco-evolutionary dynamics, then I will happily extol their virtues in all future attempts opportunities. More generally, an experiment such as that suggested here would help show other evolutionary biologists and ecologists that the study of behavioral types is important for our understanding of eco-evolutionary dynamics.