Note from Jeremy: This guest post is by Britt Koskella, currently a NERC Postdoctoral Independent Research Fellow at Exeter University in the UK. Before that, she did her PhD at Indiana University with Curt Lively, and held an NSF international fellowship. She works at the ecological end of evolutionary biology, mostly on host-parasite coevolution, combining field and laboratory work. And she does a bit of blogging and is active on Twitter.
Both Meg and I are big fans of her papers, so we invited her to talk about whatever she wanted to talk about. She picked a topic near and dear to my own heart, the value of microcosm studies for ecology and evolution. We’re hoping that Britt will write more for us in future, so enjoy the first of what will be multiple posts from her.
Thanks to Jeremy, Brian and Meg for inviting me to write a guest post here, and for all the hard work they put into keeping up such an excellent blog. In his initial email, Jeremy suggested that (although I could choose any topic of my choice) I might consider “how microcosm studies, and model system-based studies more generally, are perceived in evolution vs. ecology.” I must admit that I had no idea there was a subgroup of ecologists who take issue with microcosm-type studies until I read the papers and blog posts Meg and Jeremy suggested. (I guess I have really lucked out with reviewers!) Indeed, the recent article that Mike Brockhurst and I wrote for TREE  on the power of experimental coevolution did not include any defensive language whatsoever, primarily because we did not think the approach needed to be defended. So I decided that, in this post, rather than responding to standing criticism regarding experimental microcosm approaches in ecology and evolution, I would just lay out my naïve enthusiasm for them.
When I read theory papers, I think hard about whether I agree with the assumptions being made that underpin a given model. There are always assumptions. For example, some evolutionary models assume that selection and epistasis are weak (so-called quasi-linkage equilibrium) in order to arrive at an analytical solution. This can work sometimes, but I am always skeptical of the results of these models until I see them backed up by simulations in which selection and linkage disequilibrium matter. All evolutionary and ecological models make assumptions because they are trying to capture biology in a way that is both intuitive and meaningful. The assumptions are often laughable for those of us who study natural systems, but we stop laughing when a complicated phenomenon can be explained in a very simple way. The key point here is that no one (I hope) would argue that theory is useless because it glosses over interesting biology. Indeed, I would say that theory is useful precisely because it does just that. When a very simple model can explain a very complicated phenomenon (such as the maintenance of sexual reproduction) despite all of the assumptions being made, it is among the most satisfying types of papers to read. Am I then convinced that we don’t need data from the real world? Of course not. Can I then design a better and more informed study in the real world with which to examine this phenomenon? Most certainly.
So let’s apply the same logic to microcosm studies. Every scientist appreciates that the world is complicated. Too complicated to be fully explained by models or simulations or even our most sophisticated of statistical approaches. However, within that complexity are some really nice, simple processes that can lead to certain patterns, but which sometimes do not (i.e., when other processes are at work as well or given the stochasticity of nature). As a scientist, my approach has always been to ask first about patterns in nature, and then to see whether I can generate that same pattern in the lab using as few processes as possible.
For example, when I started my PhD with Curt Lively I was enthralled with the great data that he, Mark Dybdahl, and Jukka Jokela had collected from snails and trematodes living in lakes in New Zealand . They had shown (and continue to build on this great evidence) that trematode populations are constantly evolving towards increased infection success on the most common snail host genotypes in the population. Since these trematodes castrate their hosts, this then selects against these common host genotypes and gives rare hosts the advantage. These data are exciting for two reasons: 1) they suggest parasites can maintain genetic diversity in their host populations, and 2) they reinforce the theory suggesting that parasites confer a strong advantage to sexually reproducing hosts over those reproducing asexually (as the latter will not be able to generate rare or novel genotypes as readily to escape the coevolving parasite population).
The alternative interpretation for this result is that something else (be it the abiotic environment or another biotic selection pressure, such as fish) is driving change in the host population, and that the parasite population is simply adapting to that change. To rule this out, we needed to move into the lab, so that’s what Curt and I did . We brought a subsample of snail and trematode populations into the lab, divided them into 16 cattle tanks and allowed them to either evolve or coevolve over five and a half years, whilst controlling for all other abiotic and biotic selection. The results confirmed the pattern seen in the field; tanks that were given parasites year after year had lower frequencies of the initially common host genotype relative to those that had not received parasites. Thus we could say that the pattern of rare host advantage observed in the field could be explained by parasite-mediated selection alone.
I use this example to illustrate this point: microcosm studies are not meant to imply that the world is simple; we know it is not. They are meant to fill in the grey area between theory and nature. To test whether the amazing patterns we observe in the natural world can be explained, at least in part, by specific processes. And this is why I think they are not just useful, but imperative.
Of course, not all microcosm experiments boil things down to the simplest form, and indeed not all microcosm experiments focus on model systems. Studies that add complexity to microcosms often demonstrate that patterns found in the absence of complexity are reversed or muddled in the presence of increased complexity. For example, bacteria and phages that are coevolved in a test tube become more resistant/more infective over time, such that each retains the ability to resist/infect antagonists from the past (so-called ‘arms race’ dynamics) . However, when you increase the complexity of the system by adding in the natural community of bacteria that typically live in soil, a very different pattern emerges. In this case, bacteria are most resistant to their current phages, but do not retain resistance against phages from the past (and vice versa) . This dynamic, known as ‘fluctuating selection’, is more parsimonious with the observed local adaptation we find in the field [6,7], and it suggests that the added complexity is actually a key explanatory variable in describing the natural patterns of bacteria-phage interactions. However, we would never be able to make that statement without the initial microcosm experiment in the absence of complexity.
And the same phenomenon happens in the theoretical literature all the time, where simple models are expanded to incorporate more biological complexity and often show very dramatic differences in the outcome. But again, I would never argue that the simpler models were useless. Instead they were the key step in the process, laying the foundation for all other models to come and allowing new models to argue that it is the addition of complexity that is central to explaining the pattern. So I would argue that, just as theoretical models are working towards explaining natural phenomenon in as few steps as possible, microcosm studies are boiling ecology and evolution down to its most basic parts and then slowly adding each step together to see how much we can explain with how little. And I would go further to argue that I never fully trust a natural pattern that has been uncovered with fancy statistical models until I see the experiment to go with it (but feel free to take that apart in the comments section).
Okay, this is a long post already, so I won’t tackle the individual criticisms against microcosm studies – Jeremy has already done a fabulous job of that in his earlier post. I also realize I spend the whole post discussing microcosms, and no time at all on model systems. In part, that is because the entire argument can be remade by replacing ‘microcosm’ with ‘model system.’ If we can show that something happens in a way we expect by using a model system, this does not mean it does happen in nature in that way (or even all the time in that same system), but it does tell you that it can happen! And assuming the question being addressed is one for which a priori predictions were made based on natural patterns and/or theory, I find the results both satisfying and convincing!
 Brockhurst, Michael A., and Britt Koskella. “Experimental coevolution of species interactions.” Trends in Ecology & Evolution (2013).
 Jokela, Jukka, Mark F. Dybdahl, and Curtis M. Lively. “The Maintenance of Sex, Clonal Dynamics, and Host‐Parasite Coevolution in a Mixed Population of Sexual and Asexual Snails.” The American Naturalist 174.S1 (2009): S43-S53.
 Koskella, Britt, and Curtis M. Lively. “Evidence for negative frequency-dependent selection during experimental coevolution of a freshwater snail and a sterilizing trematode.” Evolution 63.9 (2009): 2213-2221.
 Buckling, Angus, and Paul B. Rainey. “Antagonistic coevolution between a bacterium and a bacteriophage.” Proceedings of the Royal Society of London. Series B: Biological Sciences 269.1494 (2002): 931-936.
 Gómez, Pedro, and Angus Buckling. “Bacteria-phage antagonistic coevolution in soil.” Science 332.6025 (2011): 106-109.
 Vos, Michiel, Philip J. Birkett, Elizabeth Birch, Robert I. Griffiths, and Angus Buckling. “Local adaptation of bacteriophages to their bacterial hosts in soil.” Science 325, no. 5942 (2009): 833-833.
 Koskella, Britt, John N. Thompson, Gail M. Preston, and Angus Buckling. “Local biotic environment shapes the spatial scale of bacteriophage adaptation to bacteria.” The American Naturalist 177, no. 4 (2011): 440-451.