My first paper was from my undergraduate honors thesis; it was a protist microcosm experiment (Fox and Smith 1997). Almost 20 years later, protist microcosms are still my main study system, because they remain the system best suited for answering the questions I want to ask.
Which as best I can tell makes me almost the longest-tenured “microcosmologist” in the history of ecology, and one of a very few to spend my entire career using microcosms as my main study system.
Which is a bit surprising. After all, protist microcosms have some features that you’d think would make them broadly attractive to a lot of people. They’re cheap and easy to learn, set up, and run. You can get long-term data (hundreds of generations) in a single summer. Etc. And a decent number of people have dabbled in them. So why don’t more people make a career out of them? More broadly, what makes for a “fruitful” study system in which lots of people will spend their entire careers?
Maybe the lack of career protist microcosmologists just goes to show that artificial or “unnatural” systems aren’t popular in ecology. But that just changes the question to why not. After all, there are other artificial study systems in ecology that have been more popular than protist microcosms. Think cattle watering tanks (“mesocosms”). Or think of evolutionary biology, a field in which plenty of people have made entire careers out of growing fruit flies in bottles or bacteria in flasks.
The greater prevalence of career microcosmologists in evolutionary biology may in part be a historical accident, to do with Drosophila being the model system used by the founders of classical genetics. But I don’t think that’s the whole explanation. Popular model systems don’t stay popular just out of force of habit.
Maybe the rarity of career microcosmologists in ecology is to do with a widespread aversion to “model systems” in general, or a widespread preference for system-first rather than question-first research, or most ecologists just liking to work outdoors? I dunno, I have no idea how true any of those are (well, the last one is very true). But we’ve talked about those hypotheses before. So for the rest of this post I want to think out loud about more interesting hypotheses for the rarity of career protist microcosmologists in ecology. Think of this as me playing devil’s advocate against myself.
You could argue that lack of career protist microcosmologists in ecology reflects lack of standardization of microcosm methods, the way there are many standardized methods for model organisms like C. elegans in other areas of biology (Altermatt et al. 2015). I don’t buy it, I don’t think lack of standardized methods holds protist microcosmology back. Nor do I see much potential for standardization of protist microcosm methods (sorry Florian!)
Maybe the lack of career protist microcosmologists in ecology shows that microcosms are not that “fruitful”, or once were fruitful but now are mostly played out? That is, perhaps it’s difficult to come up with a career’s worth of interesting questions that protist microcosms are good for answering, and that haven’t already been asked in that system? This possibility is at least worth considering, if only as a form of mental discipline (it’s all too easy to just assume everything is awesome about your own study system). Working with organisms that are too small to measure, mark, and track individually, and that have very simple life histories, rules out lots of questions as intractable or nonsensical. And the field ecology of most free-living protist species is little-known, so you can’t really do microcosm experiments integrated with field observations and experiments, the way somebody like Meg or Britt Koskella can with other organisms. It’s telling that many model systems in evolutionary biology are model systems for a wide range of questions, and so have entire subfields built around them. That’s perhaps particularly true for “field model organisms” like Caribbean anoles and threespine stickleback.
Maybe protist microcosms are less fruitful than other study systems because the results they yield are too clear-cut, therefore inspiring tidy conclusions rather than further questions? Maybe fruitful study systems, the ones one can spend an entire career productively studying, are the messy ones? Personally, that’s not my experience with protist microcosms at all. Yes, sometimes the results of protist microcosm experiments are beautifully clear-cut, and the possibility of obtaining such results is one motivation for using the system, but such results are far from the rule. My experience is that protist microcosms have an ideal level of messiness. They throw up “tractable surprises”. See this old post for more on this, and this interview with Rich Lenski for discussion of optimal messiness of study systems in an evolutionary context.
Then again, I think it’s really difficult to judge how inherently “fruitful” a study system is, or when it’s been “played out”. I recall back in the early oughts, I had a conversation with a very sharp colleague who questioned whether Rainey & Travisano’s Pseudomonas system (a famous lab-based model adaptive radiation) wasn’t already played out. All the low hanging fruit had been picked, hadn’t it? Yeah, not so much. Or think of how Rich Lenski himself once seriously considered shutting down the LTEE to go work on digital organisms full time, presumably because he thought the latter would be more fruitful. I suspect that fruitfulness of study systems, like life itself, can only be understood backwards.*
I also suspect that fruitfulness of a study system is a function at least as much of the investigator as the study system, or really of an interaction between the two. I once wrote that techniques aren’t powerful, scientists are. I’d say the same about study systems. So I wouldn’t infer lack of fruitfulness of microcosms from lack of career microcosmologists.
A few personal remarks on that investigator x study system interaction…my experience is that protist microcosms as a system lend themselves to fairly discrete, “medium-sized” questions. Questions that are big enough to be interesting to a broad range of ecologists, but small enough to be addressable with a single experiment, or perhaps a single experiment plus a couple of side experiments. Which suits me to a T, because that’s the way my mind works: lots of medium-sized ideas rather than one Big Idea. But I have no idea if that makes me unusual. My own research career may feel to me like it’s comprised of more discrete, one-off papers than is typical for the average ecologist, but maybe that’s just how it feels to me? Maybe to others it looks like a typical mix of sustained lines of research and one-off side projects?
Or maybe the fact that I’ve stuck with microcosms as long as I have, while others have moved on, just shows that in some ways I’m a hedgehog rather than a fox. I have an old post on that.
*Dynamic Ecology: come for the data management advice, stay for the Kierkegaard quotes.