The loneliness of the career microcosmologist

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.

28 thoughts on “The loneliness of the career microcosmologist

  1. In the unlikely event anybody but me cares: I think the only career-long protist microcosmologist with a career as long as mine is Owen Petchey. Peter Morin has been in microcosms a few years longer than either of us, but worked in ponds and mesocosms for years before that. Lin Jiang has been in microcosms his whole career but he’s a few years younger than me. Phil Warren worked in microcosms for at least 15 years if memory serves, but focused on other systems before and after that. And there are lots of people who’ve worked in them for periods of up to 10 years or so: Sharon Lawler, Marcel Holyoak, Leo Luckinbill, G. F. Gause, too many others to list…

  2. I think you’ve raised an interesting question, particularly given the foundational importance of Gause’s work to early ecological research. But perhaps that’s part of the answer – that many ecologists perceive microcosms (wrongly) as “old fashioned”?

    On a related topic: what’s the longest time that a hermetically sealed microcosm has been sustained, with all (or most) species still surviving? I’ve occasionally thought that it would be really interesting to set up such systems with different combinations of plants and microbes, and see how long they could sustain themselves as closed systems. But it’s like planting trees, the best time to do it would have been 20 years ago🙂

    • “But perhaps that’s part of the answer – that many ecologists perceive microcosms (wrongly) as “old fashioned”?”

      Huh. That never occurred to me. Offhand, I don’t think so. If only because I’ve never seen anyone say that to me in print, not even in anonymous peer reviews or grant reviews.

      “…given the foundational importance of Gause’s work to early ecological research.”

      Gause’s work is in the textbooks, of course. But I don’t know that I’d call it “foundational”. Not if you mean “foundational” in anything like the sense that Darwin is foundational for evolutionary biology, or Muller is foundational for genetics. Ecology doesn’t have *any* work that’s “foundational” in that sense. Ecology as a field has always been an slightly uncomfortable amalgam of quite different intellectual threads and research traditions.

      “On a related topic: what’s the longest time that a hermetically sealed microcosm has been sustained, with all (or most) species still surviving? I’ve occasionally thought that it would be really interesting to set up such systems with different combinations of plants and microbes, and see how long they could sustain themselves as closed systems. ”

      It’s been done. NASA types are interested in this because of the implications for sustaining an ecosystem on a spacecraft or in a biodome on another planet. Not sure offhand how long the longest-lasting ones go, but the answer’s measured in years. Heck, I think you can buy novelty paperweights that have a little mini-ecosystem inside them, that last for a year or more. What I think would be more interesting would be to ask if you could do better by, e.g., seeding them with a more diverse mixture of species initially. As opposed to trying to *engineer* just the right mix of species and culture conditions for long-term sustainability.

    • There are very old, sealed in glass pond scum microcosms that have been at UT Austin EEB since the 60’s. I forget who started it, but Mathew Leibold would know. The person who has them really wants someone to sample them!

  3. Another hypothesis: microcosms don’t show up in textbooks. All sorts of other types of systems show up in textbooks to illustrate various points. I don’t think I’ve ever seen microcosms mentioned in an ecology textbook. If you’re a student thinking about what sort of things interest you, if you haven’t encountered it, you’ll likely just start off in another direction.

    Another hypothesis: random drift. Systems drift in and out of popularity at random. Microcosms are at an ebb right now for no particular reason.

    My guess is that microcosm work is tied closely to theory and theory is not terribly popular in ecology. And even if you get cool result with microcosm work, ecologists are *always* going to demand that you show that it matters in “real” communities. Tilman started out with an algae system back in the day, but switched to terrestrial plant communities because people wondered how much his algae results were “real” with respect to communities they were more familiar with.

    • “Microcosms are at an ebb right now for no particular reason.”

      Careful–lack of career microcosmologists is different than the popularity of microcosms because many people dabble in the system or use it for a time. Microcosms right now (including not just protist microcosms but also things like Brett Melbourne’s flour beetles) are probably as popular as they’ve ever been in ecology:

      And yes, Dave’s famous for moving into grasslands to satisfy people complaining that algae in chemostats weren’t “real”. Although on the other hand, Peter Morin moved into microcosms from cattle tanks of amphibian larvae because the questions he wanted to ask were to do with population dynamics. Peter didn’t want to do single-generation experiments and then just wave his arms about what they implied about population dynamics (which lots of people do). Nor did he want a system in which experiments of the sort he wanted to run would be impossible. I think both decisions were the right ones, given Dave’s and Peter’s goals. The key thing is to ensure that the question and the means of answering it are well-matched.

      • “Careful–lack of career microcosmologists is different than the popularity of microcosms because many people dabble in the system or use it for a time. Microcosms right now (including not just protist microcosms but also things like Brett Melbourne’s flour beetles) are probably as popular as they’ve ever been in ecology.”

        Oh, in that case, new hypothesis: most ecologists these days use more than one system for asking questions, and those who stick with a single system for an entire career are fuddy duddies.🙂

      • “Oh, in that case, new hypothesis: most ecologists these days use more than one system for asking questions, and those who stick with a single system for an entire career are fuddy duddies.🙂”

        I have deep expertise in my chosen study system. You are a hedgehog. He is a hidebound fuddy-duddy.🙂

        Conversely: I am a Renaissance man. You are broad but shallow. He is a dilettante.🙂

        In seriousness, this raises the question of what counts as “one system”. For instance, does Meg work in just one system (“Daphnia and their diseases”)? Or several systems, because she does field observations of Daphnia, laboratory microcosm assays and experiments on Daphnia, genetics of Daphnia, and mathematical modeling of Daphnia?

        Also, if I ask the same question in more than one system, does that make me broad or narrow? (“yes”) Conversely, if I ask multiple questions in the same system, does that make me broad or narrow? (“yes”)

  4. Sometimes I don’t think we need to go past the less interesting hypotheses. “ecologists just liking to work outdoors”, in my opinion, probably accounts for most of it. When students are assorting themselves among disciplines, ecology draws a big chunk of the ones who love to be outside in wild nature, and a very small number of those attracted to elegant theoretical ideas. It’s the latter for which model systems are well suited, but unless your model system is the Galapagos Islands or bighorn sheep, most students who chose ecology aren’t all that interested. And if students aren’t interested, I can’t run a lab with that system for long. And it’s not just being “outside” – e.g., dandelions in lawns don’t draw interest from students either. It’s some part of nature that is beautiful or remote or wild or super diverse or all of the above. The art, then, is how to tackle Big Questions in systems people actually want to study.

    • Oh, I’m sure you’re right that it’s mostly just ecologists liking to work outdoors, and conversely mostly not being drawn to the field because of an abstract interest in Big Questions. I just wanted an excuse to wave my arms about “fruitfulness” of study systems and be a little self-critical.🙂

      “And if students aren’t interested, I can’t run a lab with that system for long.”

      That’s a constant struggle for me–keeping my lab going. For a while, I’ve been dabbling in alpine plants, and its no surprise that that’s the system that most prospective students mention when they contact me. But I’ve decided it’s not a system I want to move into full time, and that I can’t sustain working in part time, so I’ll probably wind that line of work down at some point. Likely at some cost to my ability to attract students.*

      “The art, then, is how to tackle Big Questions in systems people actually want to study.”

      Yup. Which is a slightly depressing thought, at least to me. Because it really limits the relevance of half the stuff I blog about. All my stuff about choosing a system, the value of model systems, strengths and pitfalls of different research approaches, importance of this or that subtle theoretical point, etc.–all that stuff is of only limited relevance to many (most?) ecologists and ecology students. Who have already made their choices on a lot of that stuff–or don’t even care about that stuff–thanks to just doing what they enjoy. That isn’t to say that most people are doomed to fail at the art (and that is the right word, I think) of tackling Big Questions in the systems they enjoy working in. But it does limit the relevance of a lot of the general-purpose “artistic” advice I try to offer. What most people probably need is more system-specific “artistic” advice. What Big Questions can actually be asked in a sensible way in this particular system, and how?

      *Probably the most hilariously wrong thing I’ve ever read in a scientific paper is Steve Carpenter’s (1996) worry that a whole generation of students is being trained as microcosmologists and so being lost to field ecology. There are many sins of which we microcosmologists could be accused, perhaps even plausibly–but *convincing lots of prospective ecology grad students who would otherwise work outdoors that it would be more fun to work indoors* is not one of them. Because believe me, I’ve tried!

    • A further thought, to which I don’t know the answer: if you’re right, what does that say about the future of urban ecology? Which I don’t think of as a distinct subfield, just as a potentially great opportunity to ask interesting fundamental questions in a way that also has some applied angle or at least some more direct connection to regular people’s everyday lives. Your dandelion local adaptation work is a great example.

      Now I want to ask my urban ecologist and urban evolutionary biologist friends if they struggle to attract prospective students, or attract them easily only to work on certain charismatic species (e.g., birds, yes; dandelions, no), or what.

      And a final thought: in talking recently to a colleague who recently changed universities, I was interested to hear that the institution on your letterhead makes a *big* difference to the ease of attracting prospective grad students. I mean, I’d always assumed that was the case, but it was interesting to hear it confirmed, and that (at least in this case) it’s a really big effect. If you’re at Big Famous U, it’s a lot easier to attract grad students than at Obscure U or Less Famous U.

      • Pondering system choice, subtle theoretical points, etc., seems like it should be important for everyone, if only to think carefully about the consequences of having chosen a given system.

        Urban ecology seems likely to appeal to a large subset of ecologists, given that it’s the primary habitat of most people. Finding and studying bits of nature at home is a draw (to me anyway).

        In my experience, the institution on the letter head makes a _huge_ difference to the number of the topic prospective students out there who come knocking. No question.

      • Re: the institution’s role in attracting prospective grad students, it certainly played a role in my search. As I recall, my search method was a combination of contacting individuals whom I knew were doing work I found interesting, and scanning the lists of people at “top” programs to see if any were doing work that sounded interesting to me.

        Though in the end I ended up in the lab of someone I’d have missed with both those methods, because my undergrad adviser knew Peter Morin and his then-new line of protist microcosm work, and suggested I contact him.

      • My group has done some urban ecology and has more planned in the future, specifically the role of urban settings in supporting pollinator populations and the impact of large building developments* on local biodiversity. It’s a topic that certainly interests some students who want to get out of the lab and do field work, but not necessarily head out to the wilds, and find the ease with which they can get to “field sites” appealing. That could be for a range of reasons, e.g. family commitments, disability, or just the fact that they are more “urban” individuals.

        *Actually our new university campus which is being built as I speak:

      • As somebody still early career (graduated with my B.S. four years ago, and will likely be starting my M.S. next year), and works in a lot of rugged outdoor systems (carnivore ecology primarily), I wouldn’t understate the importance of what the blog does. While the questions I work with aren’t necessarily theoretic minutia, the concerns and ideas you list on this blog are applicable to what we do because we work with data and want to find out the (approximate) truth.

        At the top of my head, the post on statistical machismo and AIC has emphasized in my mind the importance of reporting effect sizes. I’ve thought about your phase synchrony experiments and whether dispersal could have some level of counterproductive behavior in carnivore populations (outside of the commonly indicated genetic benefits).

        One other thought: you never know what minor point could blow up into a big impact. The idea that landed Feynman the Nobel Prize (which, incidentally, he almost refused because awards and honors weren’t really his style) came about when he watched somebody throw a plate through his university’s cafeteria. He started to play with equations to describe the plate’s motion, and that lead to breakthroughs in a scientific problem he was working on.

        That is, I think that the general advise this blog gives is of paramount importance *because* it’s general, and can in its own way apply to many systems.

    • The “ecologists as people who work outdoors” concept, and potential links to STEM diversity, is something I’ve been thinking about for a while.

      For someone who grew up in an urban area without much exposure to nature, maybe microcosms could actually be seen as a great system. They are a way to do ecology research without having to risk scorn because you’ve never been hiking, don’t have access to a car to get to the field, can’t afford the “right” clothes, etc. (I grew up in big cities in a family that only rarely hiked and never camped. Even though I have been spending more time with nature since becoming an adult, I still felt a bit out of place at the field station I worked at recently.)

      A lab system might also be a lot more manageable for people who have to provide part-time care to others, have a disability, etc.

      • A prospective grad student I’m recruiting at the moment is interested in my lab in part thanks to having been through a lot of physically uncomfortable (and in some cases at least potentially dangerous) field experiences as an undergrad. The sort of thing that I think many field ecologists embrace or at least shrug off-but which not everybody can shrug off. For some (rare) ecology students, the idea of doing interesting science in a comfortable, safe indoor environment is an attraction.

  5. As someone who cultures weird protists from the wild for a living, I was wondering why there wasn’t more out there on what happens in a given crude-ish culture (say, in a tube/flask or in a system with regular transfers between tubes/flasks) both in terms of community structure and the biogeochemistry involved. It’d be nice to not work with a black box, but seems like microbial ecology is either done at a large scale (some ocean basin or lake system) or hardly extends beyond classic Paramecium-Didinium experiments. So I hope this is some encouragement despite the loneliness — some of us do need your work! =)

    (In particular: how are anaerobic conditions attained and maintained (and then lost) as the prokaryotic and eukaryotic community structures shift? How is this further affected in chemically crazy conditions, like high salinity or pH levels that should be inhospitable to life but aren’t?)

    Cheers from a fellow protistologist,

    • Cheers for this, though I confess that “hardly extends beyond classic Paramecium-Didinium experiments” might well describe a lot of what I do! I just did a Didinium-Paraecium experiment (with spatial networks of patches, so it wasn’t just a replication of Gause…)

  6. I think microcosm research is having a renaissance. I can’t speak to “why aren’t there more people who ONLY do microcosms?” I think the answer to that question is that people like to approach ecological questions from more than one angle. However, if you can let that slide, I think you’ll find that a lot of people are increasingly finding your work of value.

    I work as a microbial ecologist trying to link microbial ecology to ecosystem ecology. This has led me to field experiments, theoretical modeling, and macro-ecology of microorganisms. For my post-doc I have begun developing my own model system: tiny pine plants in tiny boxes of soil paired with different mycorrhizal fungi. We can run experiments manipulating the identity of different fungal symbionts, the timing of fertilization, while using isotopes to track everything going on in a super replicated fashion that gives the statistical power a field experiment could never have. These experiments are super contrived. The soil-plant-microbe pairings certainly don’t generalize to all of nature. However the replication, paired with the low rep-to-rep variability within treatments allows us to really leverage new molecular techniques (especially since our introduced microbes have fully sequenced genomes). Our signal to noise ratio is much higher. Surprisingly, ecosystem ecologists are super into it. A lot of people see the value of the work. Vitousek’s work on the Hawaiian islands transformed how people understand nutrient limitation of ecosystems, despite the fact that Hawaii does not generalize to most of the Earth. I think people are starting to realize to get a handle of the potential power of new molecular techniques in the ecosystem context, microcosms may be incredibly useful. I also think this generalizes beyond realizing the power of molecular techniques. As someone who does field experiments, macro-ecology, and theoretical modeling I certainly see the value. While I don’t know how to address nuances of your argument about ONLY doing microcosms, I think they are certainly coming back in favor, because they allow us to do the things you described as transformational for other fields (Richard Lenski’s work, for example).

    I think the real question is, what does it take for a model system to have value beyond itself? I feel I only have half of an understanding of what the answer to that question is.

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