The microcosm wars are long since over. The microcosmologists won.

Back when I started grad school, I was acutely aware that I worked in a system–protist microcosms–that some ecologists didn’t like. When Ecology devotes an entire special feature to what, if anything, your research approach has to offer, you get quite defensive about what you’re doing and why you’re doing it, even if most of the papers in the special feature are pro-microcosm. At least, I did. After all, if it was obvious that microcosms were worthwhile, Ecology would never have devoted a special feature to explaining or debating the obvious. Hence my multiple posts defending my life, my jealousy that evolutionary biologists working in microcosms don’t feel the same defensiveness, and my interest in writing papers so as to anticipate potential criticisms. And hence my sensitivity to anecdotes that tend to support my defensiveness. For instance, Charley Krebs’ call for a moratorium on microcosm studies in ecology, to which I responded here.

But while it’s understandable that I feel as I do, what if it’s not really justified? What if the microcosm wars are over, my side won, and I just haven’t realized it?

I ask because recently, I realized that I haven’t actually felt defensive about my use of microcosms for years. Nowadays, when I read a blanket objection to microcosms like Charley Krebs’, my reaction is to sigh and roll my eyes, not feel threatened. My papers no longer routinely include long paragraphs justifying microcosms as an approach, though I don’t recall ever consciously deciding to stop including them. Thinking about it, I can’t recall ever having a paper go unpublished, or end up in a much lower profile venue than I thought it deserved, because of anti-microcosm reviewers. Heck, I can’t even remember the last time a reviewer of one of my papers or grants objected to my use of microcosms. As far as I know, It’s been yonks since anybody’s published a peer-reviewed opinion piece with blanket objections to microcosms. Conversely, there’ve been several opinion pieces in the last 10-15 years advertising the virtues of microcosms. And over the years, several friends who use microcosms have gotten grants, published lots of papers, gotten tenure, etc.

In short, yeah, it looks to me like the mid-90s microcosm wars are over and my side won, without me really noticing!* Which raises the question: when did we win?

The answer seems to be: more or less instantly! Below are Web of Science data on the annual number of microcosm papers published in leading fundamental ecology journals.** Those papers of course differ in various ways, but for convenience I’m going to do something I don’t really like and just lump together all “microcosm” papers. Anyway, there’s a big jump around 1996 to an average of 20-ish microcosm papers/year in leading fundamental ecology journals. That’s been sustained ever since, with random ups and downs of course. 1996 is the same year as that Ecology special feature on the value of microcosms. Apparently, the war on microcosms, if there ever was one, was over as soon as it began!

microcosm papers in leading fundamental ecology journals

Papers on the topic microcosm* in leading fundamental ecology journals, 1902-2016. This search picks up all papers with “microcosm” or “microcosms” in the title and/or abstract. Microcosm papers suddenly become much more common in the mid-90s.

It’s harder to search for ecological microcosm work in leading biology and general science journals, because they publish many non-ecological papers containing the word “microcosm”. But I had a go at searching on papers with “microcosm” and/or “microcosms” in the title and/or abstract, and that also included at least one of a bunch of ecological terms in the title and/or abstract (e.g., words starting with “ecolog”, “biodiver”, “metapop”, etc.). Here’s what I got:

microcosm papers in leading general science journals

Microcosm papers in leading biology and general science journals (Science, Nature, PNAS, Proceedings B, Phil Trans B, Curr Biol), 1990-2016.

Microcosm papers have appeared every year but one since 1995, which to my eye is consistent with the jump in microcosm papers in leading general ecology journals at that time.

And if you look at the time series of NSF DEB awards with “microcosm” in the title or abstract, here’s what you find:


NSF DEB awards (all programs, but the large majority are standard grants) to microcosm work, 1987-2016. Two awards from the 1970s not shown.

Microcosm awards have consistently been a part of NSF DEB’s award portfolio since 1987, with a spike in the mid-90s and a bigger spike recently.

But, but, but (I like to imagine someone saying), Steve Carpenter’s 1996 broadside against microcosms is a minor classic! Cited consistently since it was published and now up to 341 citations! True enough. But have you looked at how it’s cited? I didn’t do a formal count, but at a glance it looks to me like at least half of its citations are from microcosm papers. And some substantial fraction of the rest are from papers that aren’t even about microcosms, or at least don’t look like critiques of microcosms just judging from their titles. So yes, Carpenter 1996 absolutely lives on–but primarily as a punching bag. It gets cited by microcosmologists who then go on to shoot it down.

Ok, before anyone complains that this story doesn’t jive with their own experience: I freely admit that coarse data like these don’t–can’t–tell the full story of ecology’s changing collective attitude toward microcosms. For instance, these data can’t reveal microcosm papers and grants that got rejected because of ongoing blanket hostility to microcosms. And even if these data do more or less get that story right, no individual’s experience is going to line up perfectly with the collective experience. Heck, as I said at the outset, these data don’t jive with my own felt experience of ecology from the mid-90s through mid-oughts. Back in 1996, I definitely didn’t feel like I was on the winning team. And I wouldn’t say those feelings were totally unjustified. Just speculating here, but maybe one reason microcosmologists won the war, and won so quickly, is precisely because we felt like we were at war, and so worked hard to do good science and explain what made it good. And of course, probably our strongest argument wasn’t an argument at all–it was data. Outstanding empirical papers like Lawler and Morin 1993, Warren 1996, Holyoak and Lawler 1996, McGrady-Steed et al. 1997, Naeem and Li 1997, Kaunzinger and Morin 1998, and many others win people over in a way that no abstract argument ever does, even if it deserves to. We’ve talked about this on the blog a lot lately.

So here’s the lesson I’m taking away (your mileage may vary): yes, there are still some ecologists out there who don’t like microcosms. But there are people who don’t like ice cream too.*** I don’t think you should judge how accepted something is by the existence of a few people who don’t like it. Especially in science; no two scientists agree with one another 100%. So yes, I might get unlucky and get a microcosm paper or grant rejected because a microcosm-hater reviewed it. If and when that happens it’ll suck and I’ll probably get frustrated, just as anyone would about any bad review. But that’s not likely enough to be worth worrying about. And who knows, maybe that paper or grant would’ve gotten rejected anyway. After all, most submissions to leading selective journals get rejected for one reason or another, as do most grant applications to NSF. So as a microcosmologist I’m now going to respond to blanket objections to microcosms by channeling my inner Taylor Swift.****🙂 Again, just my own attitude.

I’m now wondering if this little story generalizes. For instance, I bet a lot of people doing meta-analysis or other synthetic work based on data collected by others felt pretty defensive in response to Lindenmayer & Likens’ recent attacks, or occasional comments in a similar vein from other prominent ecologists. And understandably so. But here’s the thing: are people who think like L&L really sufficiently numerous to have a material effect on the direction of the field? I mean, NCEAS is massively-successful and widely-imitated, and many of its former postdocs have gone on to faculty positions. Data sharing is now required by many journals and funding agencies, in large part to facilitate meta-analyses and other data syntheses. Some of the most prominent people in ecology have based their entire careers on data synthesis, something that’s never been true before. Etc. As another example, think of Travisano and Shaw’s 2012 attack on QTL mapping in evolution. I’m no expert, but I’d be very surprised if it had any effect on the popularity of that approach. I’m tempted to suggest a rule of thumb: when someone senior publicly attacks the value of some new or new-ish approach to science, it’s not a sign that the approach is under threat. Rather, it’s a sign that the approach is already too well-established to be threatened. Another illustration that scientific ideas, unlike pop stars, hardly ever die before their time.

*Clearly, we should’ve had a victory parade or something.

**Ecology, Ecology Letters, Ecological Monographs, American Naturalist, Journal of Animal Ecology, Journal of Ecology, Oikos, Oecologia.

***Obviously, one’s choice of research approach isn’t as subjective and beyond criticism as whether one likes ice cream! But that’s not the point of the analogy. Work with me here.

****Try getting that image out of your head.🙂

13 thoughts on “The microcosm wars are long since over. The microcosmologists won.

  1. That’s intriguing, seems to be another example of a step-change in the rate of ecological research in a particular area in the 90s – what I termed a “cliff” in a post from 2013:

    Simon Leather found a similar pattern:

    So, a question for the main thrust of your post – was the Ecotron money well spent? I remember visiting it just after it opened and being less-than-convinced that the price tag (was it £6 million?) was excessive. Not sure if that feeling was subsequently justified as I’ve not assessed the amount and impact of the science that followed so I’d be interested in your view on it.

    • I think the Ecotron money was well spent. Both because a lot of excellent science came out of it, and because I buy John Lawton’s argument that it was “new money” that would not otherwise have gone to ecology. The very first Ecotron experiment in particular was *massively* influential. In my mind, Naeem et al.’s Ecotron work and Dave Tilman’s Cedar Creek work basically deserve joint credit for kicking off the whole biodiversity-ecosystem function subfield.

      I do think you can ask whether the Ecotron could’ve had an even longer run of excellent, influential work than it did. The management of it changed during my time at Silwood, with the scientific direction being handed off to a committee if I recall correctly. That marked the end of the Ecotron’s run of excellent, influential work, if memory serves (which it may not). But I’m just speculating, I’m not sufficiently familiar with the internal management of the Ecotron facility to really say if it had already reached the end of its “natural scientific life” (whatever that might mean), or if it might’ve kept on cranking out Science and Nature papers had it been managed differently.

      EDIT: And thank you for the links from you and Simon on sudden bursts of interest in particular research topics. I’m sure that you’d find the same bursty dynamic if you looked at biodiversity and ecosystem function. Probably metacommunities too. Probably eco-evolutionary dynamics. But of course, while it’s easy to think of examples of topics in which there was a sudden burst of interest, it’s much harder to say if any topic that becomes popular does so via a sudden burst of interest. Very interesting to think about, but I’m unsure how to study it systematically.

      • Hi Jeremy, I don’t know if you have been back to Silwood recently, but the Ecotron has been dismantled and thrown away and has been replaced with a coffee/meeting area complete with sofas. Times have changed greatly (and not for the better) since the glorious Lawton years🙂

      • Yes, I was aware that the Ecotron has long since been decommissioned, but hadn’t been aware of what was in its place.

        I suppose that means my own former lab, which I jokingly called the “protistron”, is gone. It was a walk-in controlled environment chamber in the same room as the Ecotron.

  2. I think I could probably replace microcosm with macroecology and the post would hold (albeit the dates are slightly different).

    That said, I think publishing and grants are different. Like you, I am pretty sanguine that neither field (macroecology or microcosms) is being held up by bias against publication (nor against uptake of the ideas once published). If anything, I would probably find it easier to make a case that they are overrepresented. But I think grants, at least in the US, are funded at such a low rate, that even a one-in-ten-individual type of bias can be quite detrimental. I think there is a wide sense that macroecology doesn’t really get a fair shake at NSF (which is not the same as saying there are no grants in the area). And my one and only mesocosm proposal to CFI in Canada was decidedly killed by one individual with a blatant bias.

    • Just did a WoS topic search on “macroecolog*” in leading fundamental ecology and general science journals (the same ones as in my two separate searches in the post). Not as sudden a jump in interest as in microcosms. Rather, it’s a roughly linear increase from 1 paper in 1994 (and a couple of stray papers from before that) to a sustained level of about 15/year from 2003 until today (with a few one year spikes up to 20+; 2007, 2008, and 2010 were good years for macroecology, apparently).

  3. This is fun!

    Just checked out papers with “mesocosm*” in the title or abstract in leading fundamental ecology journals. More or less linear increase from 1-2 papers/year in the mid-to-late 90s to 42 papers last year, with no sign of a plateau.

    I don’t quite buy this, since folks like Henry Wilbur, Peter Morin, etc. were doing cattle tank experiments in the 70s and 80s. But maybe they just weren’t using the word “mesocosm”? Or else WoS records get too spotty if you go too far back in time? In particular, it doesn’t have abstracts if you go back into the 80s or earlier.

    • This is what intrigued me in the my “cliff” post – why do some fields show a sudden step-change whereas others increase at a roughly linear rate? Is there always some specific trigger that produces the step-change? I couldn’t identify one for pollinat* but I suspect that there is, I’ve just not identified it.

      • Interestingly, there’s an obvious trigger candidate for macroecology: Jim Brown’s book. And the timing is right. But if it was a trigger, what it triggered wasn’t so much a cliff as a hillslope, apparently. Which I guess could be for all sorts of reasons. Maybe it takes longer to ramp up the sort of macroecologicalical work people were publishing in the late 90s and early oughts than to ramp up microcosm work?

  4. Pingback: Why do some bandwagons in ecology get rolling much faster than others? | Dynamic Ecology

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