Charley Krebs suggests we call a moratorium on microcosm studies in ecology, because their results don’t generalize to nature. He refers to this as “Volkswagon Syndrome”, claiming that, like Volkswagon cars, microcosms don’t perform they way their real world versions do.
I have huge respect for Charley, but he’s way off base on this. He’s making a common mistake: assuming that the purpose of all microcosm studies is to reproduce or predict the behavior of some particular natural system, or ‘nature’ in general. And implicitly, he’s making the common mistake that that’s the only possible useful purpose of microcosm studies. In fact, microcosm experiments have various useful purposes (just like experiments in general have various useful purposes). Charley’s objection to microcosms only applies to certain microcosm experiments, conducted for certain purposes (e.g., to estimate the value of some rate parameter in some specific natural system), and then only if the experiment in question is in fact insufficiently realistic.
Further, Charley appears to have overlooked cases in which the results of microcosm studies do generalize to nature. For instance, Fox (2007 Oikos) shows that the average strength of trophic cascades in protist microcosms is almost scarily similar to their average strength in field experiments. And Smith (2005 PNAS) shows that microcosm and mesocosm phytoplankton communities fall on exactly the same species-area curve as natural phytoplankton communities.
In passing, Charley notes that ecologists can’t wait around for another century’s worth of data to test many predictions of interest. Which is a puzzling point to raise in this context. One motivation for microcosm and mesocosm studies of small organisms with short generation times is to collect many generations of long-term data in a reasonable human time frame. Better some long-term data from studies of organisms with short generation times than no long-term data at all, surely?
Here’s my old post on objections to microcosms in ecology, and their answers, which anticipates Charley’s objection (and others). Many of the points I make in that post have been made in older peer-reviewed literature as well (e.g., Lawton 1996 Ecology). More broadly, here’s an old post of mine arguing for the value of model systems in ecology. I’d welcome the opportunity to discuss these issues with Charley in the comments, as they’re near and dear to my heart, and because comments on his blog seem to be closed now. I’ve enjoyed our previous exchanges on related issues.
More broadly, and at the risk of reading into Charley’s post something that’s not there, it seems like Charley’s objection to microcosms springs from a concern with prediction in ecology in general. His view seems to be that predicting the behavior of natural systems is so overwhelmingly important that anything that doesn’t lead directly to successful predictions of the behavior of natural systems should be discarded. Without wanting to deny that predicting the behavior of natural systems is hugely important, and that ecologists often lack what Brian’s called a “problem solving mentality”, I’d suggest that there’s more to doing good ecology than predicting the behavior of natural systems. For instance, I want understanding and explanation as well as prediction (e.g., this old post).
Further, there are many ways in which “unrealistic” models and experiments can help us understand and, yes, predict what happens in more realistic cases. False models are useful because they’re false. Unfortunately, a single-minded emphasis on predicting the behavior of natural systems shades easily into discarding lots of useful tools that help achieve that goal, but in indirect or non-obvious ways. Charley seems to have an unduly narrow view of where predictions might come from in ecology, and doesn’t note how one can combine different research approaches in order to make predictions. Taken to an extreme, a single-minded emphasis on predicting the behavior of nature leads to Robert Peters-style instrumentalism, an unsuccessful approach ecologists shouldn’t emulate. I’d rather see ecologists emulate Britt Koskella, who has a great guest post on how she combines microcosm experiments with theory, field experiments, and field observations to really nail how her study system works. See also Meg’s and Brian’s posts on the power of combining diverse research approaches in ecology, where “diverse” includes microcosm experiments. And see Meg’s post on how she won the Mercer Award by powerfully combining microcosm experiments with other approaches. Most Mercer Award winners combine different research approaches. Ruling out any approach–microcosms, field experiments, field observations, theoretical models of various sorts, etc.–seems like a bad idea. It’s like obliging someone to fight with one hand tied behind their back. But it’s possible that I’m misreading Charley’s views on prediction.
As always, looking forward to your comments.