There’s no such thing as a mesocosm

I don’t know about those experiments.  They were all done in mesocosms…or as I call them, “bags.”

–Anonymous limnologist

Last week, the eminent population ecologist Charley Krebs, channeling the sentiment expressed in the quote above, wrote a blog post on something he dubbed the “Volkswagen syndrome” in ecology.  He points out that ecologists are bad at prediction, and wonders if our shortcomings in this department may be due in part to over-reliance on simplified models, labratory microcosms, and field mesocosm studies.  The name alludes to VW’s recent attempts to, er, “simplify” the results of their cars’ emissions tests.  Krebs wonders if we should declare a partial moratorium on microcosm studies until some kind of meta-analysis can show whether, or under what conditions, they are worthwhile.

This post drew a strong reaction from Jeremy Fox at Dynamic Ecology.  Fox does much of his work with protists in microcosms, and so I think he (understandably) felt a bit defensive about what may have sounded like an attack on his whole research program.  Fox argues that there are examples of micro/mesocosm work that have generalized to nature, and links to an older post defending micro/mesocosms against a list of common criticisms (which I get the sense he hears a lot).  Morgan Ernest at Jabberwocky Ecology also had this less-strong response to Krebs’s post.

This is all interesting, but at this point, I’m getting a sinking feeling. This debate is drifting into familiar territory for ecology.  Terms are imprecisely defined (What is a mesocosm, anyway, and what separates it from a microcosm?).  Questions edge towards false choices (Is it better to predict or to understand a natural system?) or the unanswerable (What makes an experiment worth doing?  When is a model too simple? Are mesocosms “useful?”).  Impersonal criticisms end up landing personally.  Oh boy…with a setup like this, I can’t wait for the rest of this Robust DiscussionTM

While I wait for my popcorn to finish popping, I think it is useful here–and in basically every ecological debate, for that matter–to remember couple of large facts.

The first fact is that despite the many named processes in ecology (competition, exclusion, succession, trophic cascades, etc. etc.), there are, when you get down to it, only a few fundamental biological processes.  The universal instructions for life on earth are as follows:

  1. Get born/hatched/sprouted/cloned.
  2. Assimilate matter and energy from your environment.  These often come packaged in some other tasty organism.
  3. Move around some.
  4. Produce offspring similar to yourself.
  5. Die.

There are a lot of different ways to do each of these steps, sure, but every organism does the same five. Everything else is an emergent phenomenon.  Given a little mutation and enough time, evolution happens.  At shorter time scales, you get the beautiful mess we call “ecology.”  The named processes you learned in Ecology 101 may be useful shorthand for common emergent phenomena, but they aren’t real “laws” by any means.  When we test an ecological theory, we need to be precise about what that theory means, and which of the fundamental processes are important in that situation.

The second large fact is that scale matters.  Each of those five steps for life has some rates associated with it: number of offspring per breeder per unit time, length traveled per unit time, or whatever. While these rates may depend on all kinds of different factors, we can usually estimate them within an order of magnitude (or two) pretty easily.  And even a very rough estimate can be illuminating when we discuss the usefulness or validity of a particular mesocosm or microcosm.

Take one of Fox’s protist microcosms.  It is pretty micro: the whole thing could fit in your hand.  However, compared to the critters inside, it is quite large.  And while protists and bacteria do experience spatial heterogeneity, it is small, on the scale of microns to millimeters, and is biologically generated over minutes or hours.  Their generation times are on the order of a day.  A reasonable argument can be made that the constraints of this microcosm do not matter at the scale of the organisms inside it.  Fox’s default mental picture of a microcosm is a totally reasonable model for general ecological dynamics.

Now consider snowshoe hares, one of the species Krebs has studied in depth.  They have generation times of a year, live up to six years, and move up to 20 km in their lifetime.   They experience landscape variability from the centimeter scale up to the longest distances they are capable of traveling.  Their predators have home territories of tens to hundreds of square kilometers.  It is hard to imagine a mesocosm within which the basic rates and ranges of snowshoe hare ecology would not be severely cramped. Krebs’s default mental picture of a microcosm is an idiotic simplification of a natural system that shouldn’t be expected to produce any generalizable results.

Obviously, there is no One True Way to study ecology.  Obviously, simplification is the whole point of models, model systems, and experiments. But they have to be assessed critically, based on the scale of the important rates and processes.  This is why I think the question “are micro/mesocosms useful?” is not a meaningful one. Whether something is a micro-, meso-, or macrocosm depends entirely on how it compares to the scale of the processes at hand.  There is no such thing as a mesocosm in and of itself.

These comparisons of scale must be quantitative.  Common weasel words like “landscape scale” can mean whatever you want them to.  Much better is a dimensionless ratio–for instance, “(diameter of mesocosm) / ((mean speed of organism) x (duration of experiment)).” If you don’t know what the important rates and scales are for your question, or what units they are measured in, you might want to think a little longer before launching into your experiment.

Finally, there may be ecological systems and dynamics that are just not observable or manipulable at present.  Sometimes, the variability happens too slow, or too fast, for us to measure with our current means and techniques. This was one of the main points of Henry Stommel’s famous 1963 paper, “Varieties of Oceanographic Experience,” which I have written about before: we need be honest with ourselves about what it takes to observe a given process.  There are a number of approaches you can take to an unresolvable phenomenon (they mostly involve technology, time, money, or modeling).  The only one guaranteed to fail is pretending you can measure something you can’t.

The last paragraph of Stommel’s paper is striking.  Though written about physical oceanography five decades ago, it could almost be about ecology today:

In the past there were very few points of contact between the ocean as visualized by conventional analysis of serial observations on the one hand and the ocean as portrayed by simplified laminar theoretical models on the other. I think the reason is not hard to find: neither model had been developed to a level of sophistication corresponding to the essential complexity of the oceanic phenomenon it was trying to describe…There is no harm in thinking at first about the ocean in various simple ways, to see how satisfactory a model one can devise, but a time comes when consideration of the next stage in complexity can no longer be postponed. Happily, we have the technological means to begin oceanographic observation of the new type, and we can look forward to a time when theory and observation will at last advance together in a more intimately related way.

So say we all, Hank, so say we all.

Anyway, Krebs is actually giving a seminar here at Stony Brook next week. If you’ve got questions/thoughts/accusations for him, throw ’em in the comments, and I’ll see if I can get some answers/responses/counterattacks…

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7 Responses to There’s no such thing as a mesocosm

  1. Jeremy Fox says:

    Nice post, I agree with it.

    It’s Charley Krebs who posed the blanket question of whether microcosms/mesocosms are ever useful, and claimed the answer was “no”. So if you don’t think that’s a useful question to pose, well, tell him that! Although I guess you argue that I should’ve just skipped straight to posing a more useful question, rather than first giving the correct answer to the non-useful question Krebs posed. You could also argue that I should’ve just ignored Krebs entirely. But yeah, I am sick and tired of hearing this sort of silly blanket objection to any and all microcosm studies. My probably futile hope is that my response will prove useful to students in particular.

    • Sam says:

      He doesn’t dismiss mesocosms quite that flatly. He wonders aloud about a “partial moratorium,” and says we should investigate empirically how well lab and mesocosm studies generalize to nature. (Though he does make it pretty clear what his opinion on that question is.)

      I certainly don’t think that all micro/mesocosms are useless, but I do agree with Krebs that there’s a subset of them, mostly with larger organisms, that do have serious shortcomings but are sold as informing us about conservation or management anyway. And when these issues are raised, the response is often along the lines of, “Yes, I’m aware of that issue, but for obvious practical/logistical reasons we couldn’t do any better. Ecology is hard.” The answer is true, and everyone can sympathize, but it’s also logistical answer to a scientific question.

      A better question to ask of a micro/mesocosm study is “how is this useful?” You’ve given a number of possible valid answers to that question besides “it helps us predict a natural system.” But if that is the given purpose, then I’m totally with Krebs that those predictions need to be tested empirically. Few ecologists would disagree with that…but then again, few ecologists actually make quantitative predictions, either…

      • Jeremy Fox says:

        I agree with everything you say. I just don’t think it’s much of a defense of Krebs’ post to say that it’s defensible if read generously, given that it’s *only* defensible if read generously.

        BTW, Lord knows I’ve written dud posts that weren’t clear, or that I hadn’t thought through. I have a terrible, unclear one on “getting over Robert MacArthur”. And a dud criticizing live-tweeting of talks for silly reasons. Probably others I’m not recalling. In every case, I appreciated that commenters didn’t mince words and told me firmly–politely, but firmly–that I was either very unclear or very wrong.

        But you’re right that it’d be best to move on and have the conversation we should be having–about the specific ways in which mesocosm studies conducted for specific purposes can go wrong.

        BTW, I sympathize with your point that “I know approach X is flawed, but it’s the best we could do” is a very weak defense of approach X. Shameless self-promotion alert: I have an old post on this:

        https://dynamicecology.wordpress.com/2012/10/24/no-i-dont-need-to-propose-an-alternative-approach-in-order-to-criticize-yours/

    • Luis says:

      I also agree with it. thanks for the nice article!

  2. Pingback: Friday links: Mark McPeek vs. grade inflation, Endurance, #LOTRyourResearch, and more | Dynamic Ecology

  3. Philip H says:

    So ask him straight up if he’s going to do the meta analysis to see if there is value to this approach.

    I’d also ask him what his alternative would be. Large geographic scale longitudinal ecosystem studies are hard to fund and harder to execute – if you really add it up there are probably a few dozen places worldwide that have been truly observed for understanding over a sufficient time/geographic scale as to be useful for prediction – provided you keep those predictions to that area! Absent a change in this situation, mesocosms are about all that’s reasonable left.

    • Sam says:

      I will try to ask him, I’m interested whether he has plans about this. Or how you would select studies for the meta-analysis, or define successful predictions…

      I actually think there are a lot of approaches that aren’t century-scale ecosystem studies or mesocosms that are reasonable and can help us make progress. I think mathematical theory and computer models can be really illuminating, especially if they are tested in a rigorous way against the real world. I like the ideas in McIntire and Fajardo’s “space as surrogate” paper, for instance, and Volker Grimm’s “pattern-oriented modeling.”

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