Note: This post is old wine in a new bottle. It basically repeats some old posts, just in a slightly different way. I’m only doing it because the comment threads on those old posts are really good, but I felt like they petered out a bit too soon.* This is my attempt to revive them. So if you’ve been reading my old posts on macroecology and the associated comments and thinking “More please!”, this post is for you. But if, as is more likely, you’ve been reading those old posts and thinking, “Jeebus, doesn’t he have anything new to say?”, just skip this one.
Note: Man, this post ended up way longer than I originally intended! Sorry about that. Maybe everybody should skip it. Basically, all the post does is argue that macroecology is not at all like astronomy, except in a couple of superficial ways. If you really care why I argue that, and can’t guess it from having read old posts, read on…
I write a lot on this blog about how difficult it is to infer process from pattern, mechanism from observation, and causation from correlation, even tentatively. In response, ‘macroecological’ colleagues, whose work emphasizes the documentation and interpretation of observed ‘large-scale’ ecological patterns, often point to the example of astronomy. The example of astronomy, they say, illustrates how observational science can be successful science, and even causation-inferring science.
But unless I’ve missed it (which is quite possible), they never keep following that line of thought, at least not in any detail. I wish they would. Yes, absolutely, astronomy is a successful, causation-inferring science, and it does so without being able to manipulate stars or galaxies or whatever. But precisely how does it achieve its successes? After all, there are also unsuccessful observational sciences. Macroeconomists, for instance, infamously remain in vociferous disagreement on even the most basic points. So what makes astronomy successful, and can macroecology emulate it? I emphasize that in asking this question, I really don’t know the answer and I’m genuinely curious. I’ve asked this question in the comments on previous posts, but never gotten a reply. So I decided to do a post on it, in the hopes of smoking out Brian McGill and Ethan White’s inner astronomers. 😉
Just so I don’t come off as totally lazy (“Hey readers, teach me astronomy!”), I did do a bit of background research**, the fruits of which are below.
Origins of the macroecology-astronomy analogy
The macroecology-astronomy analogy seems to originate from a comment by Robert MacArthur to Jim Brown, reported in Brown’s Macroecology (p. 21):
“Astronomy was a respected, rigorous science long before ecology was, but Copernicus and Galileo never moved a star.”
Brown goes on to cite geology, specifically the theory of plate tectonics, as a second example. That mechanistic theory is well-confirmed even though geologists have never experimentally manipulated entire tectonic plates or the mantle plumes that move them around.
Brian Maurer, in his Untangling Ecological Complexity: The Macroscopic Perspective (p. 112-113) pursues this analogy a little bit further (in fact, as far as I’ve ever seen it pursued):
“Explaining these patterns [in assemblages of species] is difficult because the standard tools of science for developing mechanistic explanations cannot be used. With few exceptions, there is no way to manipulate the biodiversity of a large geographic region. Another problem is that often the same pattern might be consistent with more than one process…[These limitations] also apply to astronomy, but this has not prevented astronomers from learning a great deal about stars and galaxies. Astronomy has a strong, quantitative theoretical foundation in physics, and this foundation allows fairly precise predictions to be made about what patterns can be expected in complex systems like galaxies.”
I can totally see why early macroecological texts pushed this analogy. It’s an effective response to anyone who would claim that, if you’re not doing manipulative experiments, you can’t possibly be doing science. But while the analogy establishes the possibility of a successful, astronomy-like macroecology, I don’t know that it establishes the actuality. Indeed, based on what little I know about astronomy, I’m skeptical of the ability of macroecology to emulate astronomy. I don’t think this means macroecology can’t be successful or infer causality–but I do think its methods aren’t really analogous to those used in astronomy. But these thoughts are tentative. I hope that people who know more than I do about astronomy (or macroecology!) will chime in.
I emphasize that I’m not actually saying that any macroecologist takes the astronomy analogy as seriously as I’m about to try to take it. Nor am I saying that they should have done so–I’m not accusing them of failing to follow their own argument to its logical conclusion or anything like that. I’m actually not out to criticize their use of the analogy at all. I’m just intrigued and curious. I want to see what we can learn by pushing the analogy as far as it will go, even if that means pushing it further than macroecologists have ever taken it.
Reasons why macroecology is not like astronomy
1. Ecologists can do experiments! Ok, it’s true that you can’t manipulate, say, the biodiversity of an entire continent. But you certainly can do smaller-scale experiments that are directly relevant to interpreting large-scale patterns. One example that I’ve raised before, and which I’ll raise again because it’s such a great example***, is the work of Jon Shurin on local-regional richness relationships in freshwater zooplankton communities (Shurin 2000, Shurin et al. 2000). After correcting for an artifact to do with variation in spatial extent of different regions, lake zooplankton appear to exhibit a linear relationship between local (within-lake) species richness, and regional richness (total richness of all lakes in a large region). This has been taken to indicate that local diversity just reflects dispersal limitation, a sort of “passive sampling” from the regional “species pool”, meaning that local communities are open to colonization by whatever species happen to arrive. But here’s the thing: local zooplankton communities aren’t open. You can directly test that by trying to invade lakes with species not currently present. It turns out that invasions mostly fail, unless you first drastically reduce the densities of resident species, thereby eliminating competition from residents. Far from being open to whatever colonists happen to arrive, lakes are almost completely “saturated”. This means that linear local-regional richness relationships had been misinterpreted. As is now well-established, linear local-regional richness relationships are one of those patterns that are, as Maurer says, “consistent with more than one process”. Small-scale experiments like Jon’s were key to establishing that point in the context of local-regional richness relationships.
So macroecologists can’t “manipulate the stars” or “manipulate tectonic plates”–but they certainly can do experiments that provide information directly relevant to the macroecological equivalents of the heliocentric theory or continental drift. In this respect, macroecologists are actually in a better position than astronomers or geologists when it comes to inferring causality. They have more weapons in their arsenal.
This is one way in which I think the analogy with astronomy might actually be holding macroecology back a bit. Their emphasis on the impossibility of large-scale, “manipulate the stars”-type experiments sometimes seems to cause them to downplay the relevance of other sorts of manipulations.**** Just because the pattern is large-scale doesn’t mean the only relevant experiments are large-scale. The underlying processes that putatively generated the pattern typically operate everywhere, at all times, and so can be tested for anywhere, at any time.
As a second example, Jon Levine and others have powerfully combined small-scale experiments with larger-scale observations to show that the large-scale correlation between native and non-native species richness is down to the fact that the same environmental conditions that promote native diversity promote non-native diversity (e.g., high rates of propagule supply). This effect swamps the fact that, all else being equal, more species-rich communities are more resistant to colonization by species not already present (Levine 2000, Levine 2001 Oikos)
Now in fairness, Ethan White has argued in the comments on old posts that all the best macroecology actually recognizes this and is based on synthesis of all relevant information, including small-scale experiments. I wish I fully shared his confidence that this kind of work is what everybody is out to do, at least ideally. I’m torn between taking his word for it (since he knows the literature far better than me), and my own admittedly-limited experience as a reviewer of macroecological papers which too often neglect directly-relevant experimental work.
2. Astronomy is based on the quantitative estimation of different effects, using well-developed and -validated physical theory. My point here is basically an expansion on Brian Maurer’s brief remark about astronomy’s “strong, quantitative foundation in theoretical physics.” What that foundation allows astronomers to do is to estimate and subtract out from their observations the effects of all sorts of “nuisance” factors and sources of error, leaving them with accurate, precise estimates of the quantities of interest. For instance, see here, here, and here for layman-level discussion of how “transits”, such as the recent transit of Venus between the Sun and the Earth, allow astronomers to accurately and precisely estimate quantities like the mass of the Sun, the absolute (not just relative) distances from the Earth to other objects in the solar system, and the chemical composition of the atmospheres of other planets. See here for the estimation of stellar parallax (a very subtle effect). And see here for discussion of how subtle deviations in the orbits of planets from what would be predicted based on Newtonian mechanics and the masses of known planets led to the discovery of new planets. Note in every case that getting a good estimate does not involve just accumulating a big sample size and then averaging away the “noise”, thereby allowing the desired “signal” to reveal itself. Rather, getting a good estimate involves using well-established,quantitative background knowledge to precisely quantify, say, the Doppler shift in the spectrogram of the atmosphere of Venus due to the Earth’s movement around the Sun.
Macroecologists certainly try to do this sort of thing. They often include covariates in their statistical analyses to statistically control particular sources of variation, they can use comparisons among different datasets to estimate error sources known to affect only some of those datasets, and they can use randomization-based “null models” to try to figure out what their data would look like in the absence of some particular process like interspecific competition. But are those approaches anything like as precise and well-validated as what astronomers do? Indeed, in the case of randomization-based null models, there are reasonable arguments that they don’t, and can’t, work at all.
Further, macroecologists often deny that we could ever have fully-parameterized models of the “microscale” processes of birth, death, and dispersal that ultimately drive species distribution and abundance. I actually don’t think that’s true, at least not universally, but let’s say for the sake of argument that it is. Doesn’t that amount to a denial that we’ll ever have a “strong, quantitative foundation” that would allow us to estimate and subtract out “nuisance” effects, thereby allowing us to precisely estimate effects of interest? For instance, if you think that it’s impossible to parameterize a many-species competition model for a large, spatially-heterogeneous area, what makes you so sure that just randomizing your observed species x sites matrix while holding the row and column totals constant subtracts out all effects of interspecific competition while leaving effects of all other processes intact? Isn’t that basically like an astronomer saying “I don’t know how to quantify the Doppler shift in my spectrogram, so I’ll just randomize my data with respect to the day of observation and hope that that fixes it?” Doesn’t this lack of what economists call “microfoundations” make macroecology more like macroeconomics than astronomy?
3. Astronomy isn’t really about statistical patterns. In a classic Oikos paper I discussed in one of my first posts, John Lawton (1999) argues that macroecological patterns reflect the fact that, at large scales, the “noise” of species- and system-specific details “averages out”. There are reasons to question whether that’s a good analogy for macroecology, but let’s accept it for the sake of argument. Here’s my question: is astronomy like that? I mean, when astronomers estimate the properties of some object in outer space–its distance from us, its chemical composition, its size, etc.–they’re estimating the properties of that particular object. Yes, they do that repeatedly for lots of objects, and I’m sure there are statistical patterns in the resulting data. For instance, maybe the “species-abundance” distribution of different kinds of stars has some sort of interesting shape? But it’s my impression that most (all?) of the vaunted quantitative, cause-inferring rigor of astronomy comes into play in estimating the properties of individual objects, not in studying the statistical features of collections of objects. Basically, I’m suggesting that, if statistical mechanics is your model for what macroecology is like (as both John Lawton and, in other passages in his book, Brian Maurer suggest), then astronomy is not. Astronomy and statistical mechanics are very different in terms of what they’re aiming to do and how they’re aiming to do it. In his paper, John imagines a fairy who foolishly tries to understand the intractable random movements of individual particles of a gas, totally missing the tractable macroscopic properties of large collections of gas particles. But predicting the highly non-random movements of individual “particles”–planets, say, or comets–is what astronomers live for!
Am I totally wrong about all this? Maybe I’m just focusing on the wrong bits of astronomy, and other bits actually are a great model for how macroecology works, or could work? Or maybe I’ve just shown that the whole macroecology-astronomy analogy can’t be pushed any further than the very short distance that Brown and Maurer push it? (Woohoo! I’ve saved macroecology from a shaky analogy no one would’ve thought of if I hadn’t suggested it!) Or in pushing the analogy further, have we actually highlighted some things that needed highlighting, such as the ability of macroecology to draw on small-scale experimental data? I’m honestly not sure–you tell me.
And then I promise to shut up about macroecology and talk about something else. 😉
*Also, right now I’m a bit low on both time for really substantive posts, and really new things to write substantive posts about. It’s quicker to repeat myself. 😉
**Specifically, I spent 5 minutes googling “astronomy blog” and reading the top hits. 😉
***I did warn you about old wine in a new bottle.
****It also causes them to forget that you can “manipulate the stars” if you create an artificial universe in which the stars are small enough to be manipulable. That is, you can do experimental macroecology in microcosms. Phil Warren and his collaborators have done a lot of nice work on this (e.g., Holt et al. 2002).
Interesting post, I had missed the previous ones, so I’m still unspoiled. A few ideas:
regarding your point 1) about experiments: in astrophysics, there is very close collaboration with small-scale experimental science, especially with experimental particle physics and plasma physics. In fact, the astrophysics – particle physics collaboration is often cited as a prime example of addressing a question (interactions of matter) fruitfully with data from two completely different scales (see e.g. http://en.wikipedia.org/wiki/Astroparticle_physics).
regarding 2) Isn’t the lack of theory rather a reflection of the state of ecological theory in general than a specific property of macroecology? Unlike physics, ecology simply doesn’t have a generally accepted micro-founded theory of how diversity emerges and distributes (we can’t even agree on the cause of the latitudinal gradient, or whether species assembly is niche-mediated or neutral). Also, I don’t have the feeling that macroecologists are fundamentally opposed to mechanistic explanations, see e.g. http://onlinelibrary.wiley.com/doi/10.1111/j.1600-0587.2012.07364.x/abstract.
regarding 3) actually, there is a lot of statistical and stochastic simulation work done regarding the evolution of the early universe, the formation of stars, etc., e.g. to explain the distribution of the microwave background http://en.wikipedia.org/wiki/Cosmic_microwave_background_radiation, and a lot of statistics on cosmological parameters as well.
I don’t find the analogy with the astro-research so bad … not sure if it teaches us much though, except for the fact that, when we want to learn something about the big bang, we have to use the observations we can acquire, and those happen to be mostly non-manipulative in astrophysics, for the obvious reason that the big bang and the formation of stars is difficult to reconstruct in a lab, and the same is true for large-scale evolution and macroecological patterns – we can do some micro experiments, but we also have to get the macro pattern to confirm our theory, there’s simply no way around it.
Whether it also makes sense to build some “thermo-dynamic” macro-theory of ecology in analogy to macroeconomics or thermodynamics is another question I suppose, but I also don’t think that there is unanimous support for that in macroecology.
Great comments, Florian. The example of astrophysics (as distinct from those bits of astronomy I focused on) and its close connection to experimental particle physics is a great one that I should’ve remembered myself. Reinforces my point about the relevance of ‘small-scale’ experiments for interpreting ‘large-scale’ phenomena.
Yes, ecology does lack the sort of microfoundation astrophysics has, and I actually doubt it will ever have such a foundation. In this respect, I definitely think macroecology is much more like macroeconomics than astronomy. It’s not that I think macroecologists are opposed to, or uninterested in, microfoundations. I just think it’s contradictory that some macroecologists express pessimism about the possibility of microfoundations on the one hand, but on the other hand use methods like randomization-based null models that implicitly make *very* strong (and often *very* implausible) assumptions about microfoundations. At least macroeconomists who believe in the importance of microfoundations are willing to specify and defend the highly-unrealistic-but-mathematically-tractable microfoundations on which their macroeconomic models are based.
Good point about statistical and stochastic simulation work on things like the evolution of the early universe. Again, I should’ve remembered that stuff.
I like your suggestion that the analogy with astronomy perhaps doesn’t teach us all that much, besides “use whatever tools you have at your disposal”. Every field faces its own unique challenges, and while some of those challenges will have analogies in other fields, we probably shouldn’t make too much of those analogies.
Agreed, although I’m a bit more optimistic about the possibility to arrive at sensible microfounded theories in ecology, but I guess this is something the future will show (btw., microfoundation is such a useful word, we should steal this from the economists)
Great discussion below as well. I have to admit that I was unaware about how contentious the observational approach of macroecology is (or was?). Actually, it seems a bit hilarious that we have to resort to astronomy to convince fellow ecologists of the value of observational science – as if we didn’t have enough examples of that in our own discipline – I’ll put forward the idea of natural selection to name only one. Sure, there has been some collateral damage in the form of senseless regressions while building macroecology, but I suspect that wounded pride might have as much to do with those attacks as any real scientific disagreement. As Brian said, Macroecology has had a formidable run in the last years, and of course this success is the loss of other sub-disciplines, or so it must seem to some.
Stimulating post Jeremy – thanks. Didn’t take you long to “smoke” me out – at least you now know I am a frequent reader of your blog!
First the big picture. I (and I presume all thinking macroecologists) think experiments are good (and as you suggest microcosm experiments are probably most relevant to macroecology). But experiments are not a “must have” to do good science. I hear a lot that macroecology is not a real science because of lack of experiments. Aside from the fact this is rude and judgemental, it is not true. As such the MacArthur quote is completley logically sufficient – an example (astronomy) of a good science without experiments is sufficient proof. No analogy claimed or needed. To me this is the spirit in which the MacArthur quote most often gets pulled out by macroecologists (and indeed I suspect the spirit in which MacArthur offered it).
As for your 2nd and 3rd points on theory and nature of theory. There are a lot of people calling themselves macroecologists running around who stop once they get their empirical regression published. But you can’t judge any branch by its worst practices. I would argue that some of the most stimulating theoretical development in the past decade has come from macroecologists. Neutral theory and MaxEnt theory are examples. Now a lot of traditional differential equation/population dynamic ecologists may not love this theory but that is a form of provincialism. I think if you for example looked at new (i.e. non-classical) theories that have inspired the most grant proposals in the past decade Neutral theory and MaxEnt would be near the top. As Florian already suggested, large swaths of physics, astronomy and chemistry depend on statistical theory and I see no reason why ecology should be any different.
Additionally wrt theory, it is instructive to look at the history of astronmy. Modern astronomy started with a boat load of data collected by Brahe. Then Kepler turned it into some simple rules about ellipses with no mechanism. In short Kepler’s name has lived on for 500 years because he found – yes – patterns! It was another 50 years before Newton turned it into a mechanism. This took about 100 years to play out. The other half Newton’s story comes from Galileo’s data on the rate at which balls rolled down a ramp – no manipulation of the gravitational constant or proximity to the earths gravity was performed – it was also “just” a pattern! Pure empiricism and pattern finding have played important roles in other (all?) fields too. Its a hard thing to do, but maybe we should give macroecology 100 years too before we judge it too harshly.
Finally on experiments and macroecology. I am a fan of experiments whenever and whereever possible. But one has to acknowledge that for very many important macroecological questions experiments are logistically and/or ethically impossible. This is because of scale. It is the exception (some of which do exist as you point out) that an experiment at a small scale can be informative about large scales. The dominant processes are completely different. It would be nice if this weren’t true but it is. I hope 20 years after Levin’s paper on scale I don’t still have to argue this. Just as a simple example, I know of no experiments that are likely to decisively weigh in on the latitudinal diversity gradient. The scales are just wrong. The latitudinal diversity gradient is driven by what controls the rate of speciation and extinction. Any experiments I can think of are going to speak to community assembly. It is possible to be clever and do quasi experiments using space for time and such tricks. Thus one of the best papers on this question in recent times in my opinion is by Powell in GEB 2007 (16:519) which looks at how the latitudinal gradient varies over a ~100 million year time scale and shows that seasonality is likely important. Cool, good science, and observational. No experiment anywhere in sight.
In this way, I do think some limited analogies with astronomy are relevant.
In summary on experiments and macroecology: good idea, not always possible, not always necessary.
I do agree with your main point – it is an open question whether macroecology is more like astronomy or macroecology. And although I don’t think it was ever MacArthur’s intention, I don’t think macroecology is highly analogous to astronomy (ecology is too complex and high dimensional).
Personally I think microcosms, paleodata and theory are the key for macroecology to move forward. But I think these judgements by people external to the field saying that macroecology is not a real science without experiments are stupid and I can’t really be bothered to spend much time on them (NB your piece Jeremy was very reasoned and friendly in tone and did not claim this – I’m not lumping you in that bucket which is why my detailed answer – but I can’t tell you how many times and places I have heard the judgemental sentiment in pretty much those exact words). More than anything, just like any other field, cleverness and penetrating thinking are essential but too rare and in that macroecology differs from no other branch of ecology. We all might be better off to give all of ecology 100 years to see where we end up before we judge it.
Thanks Brian, I’m flattered that you liked the post and didn’t just find it a boring rehash. Thanks for taking the time to comment at such length.
Thanks for confirming that, as I suspected, the astronomy analogy is merely intended to establish that experiments aren’t essential to good science. Disappointing but not surprising that not everyone finds this reply convincing.
Re: the timescale of scientific progress in astronomy and giving ecology, or any subfield of it, a century or more before we judge it: interesting, not quite sure how to respond. Contrarian that I am, my first instinct is to try to think of cases of really rapid and sustained progress in science, or cases where long periods of slow/no progress really did represent stagnation. And to think about the long-term average rate of progress vs. fluctuations around that average (analogous to “punctuated equilibria” or [progressive] “scientific revolutions”). I also wonder whether your argument here couldn’t just serve as a way to shield any field from judgement for almost arbitrarily-long periods. I’m reminded a little of Keynes’ remark that “In the long run, we’re all dead”. This remark comes in the context of a discussion of how the fact that the world economy would emerge from the Great Depression “in the long run” without any government intervention was cold comfort to all those suffering very real hardship in the present. In the same passage, Keynes also makes the analogy to a ship caught in a storm–saying that storm will eventually pass doesn’t actually tell the captain how to keep the ship from sinking before then. So while I freely grant that scientific progress can be, and perhaps even usually is, slow and intermittent, I don’t see that that should prevent us from asking hard questions about how best to do science right now.
I actually have little idea how to “judge” macroecology, or any field of science. As in any field, I see papers that are great, and papers that aren’t so great. I feel like I can judge those papers, and by extension, their authors, at least in certain ways. But I don’t feel like I, or anyone, can really “judge” any field as a whole. Not only don’t I read enough of any field, but I have no idea how to figure out how good any field “could” be or how rapidly it could realistically “progress”. As I said in the post, I’m unsure how to judge even narrower issues such as whether macroecology “as a field” takes experiments seriously enough. It’s funny, when it comes to judging scientific issues all scientists like to have lots of data, good quality data, well-developed theory, precise and testable hypotheses, rigorous experiments, etc. But when it comes to judging issues related to the conduct of science, like “Is macroecology making progress?”, or “Is peer review in crisis?” or “Do we emphasize fundamental research too much?”, we all (well, most of us) have really strong opinions based on little more than anecdotes, vague intuitions, and deep-seated-but-totally-unexamined-and-unjustified value judgments.
Fortunately, I don’t think it’s actually necessary to “judge” how well “macroecology as a whole” is doing in order to have sensible discussions about how it could be done better. I’d make an analogy to coaching sports here. As a Little League baseball coach, I don’t have to judge how good my team is in some absolute sense, or even compared to the other teams in our league, in order to identify the specific skills we most need to work on.
Re: the complexity of ecology making it more analogous to macroeconomics than astronomy, I agree. Although fortunately
macroeconomicsmacroecology isn’t riven with moral and political debates disguised as empirical debates. 😉 Although then again, debates about the importance of experiments in ecology kind of have that character… 😉
Re: experiments in macroecology being possible and useful for some questions but not others, it’s interesting that you bring up the latitudinal richness gradient. When I was in Peter Morin’s lab, Peter submitted an NSF grant to do microcosm experiments to test certain classes of hypotheses proposed to explain the latitudinal richness gradient. As I recall, basically the idea was that you couldn’t do experiments to test hypotheses based on historical contingency (like “it’s just a transient reflecting post-Ice Age recovery”), or on macroevolution (speciation and extinction rates), but you could at least test whether ecological hypotheses like “tropical areas are more productive and so support more species for ecological reasons X, Y, and Z” were viable. As I recall, the proposal got very contrasting reviews–half the reviewers totally loved it and half absolutely hated it. It wasn’t funded, and I can’t recall any details of what exactly was proposed or what exactly the reviewers said about it.
I guess I relate this anecdote as a long-winded way of saying yes, I agree that relevant experiments aren’t always possible–but sometimes lack of relevant experiments just reflects lack of imagination on our part. For instance, I think it’s great that you appreciate the relevance of macroecological microcosm experiments like Phil Warren’s, to the point of considering them a key direction for future macroecology (!) But I’ll bet that lots of even quite smart macroecologists wouldn’t have even thought of doing the sorts of microcosm experiments Phil has done. I say that not as a criticism of the creativity of macroecologists, but as a complement to Phil’s creativity.
Yeah like Jim & you I consider people who can’t see that experiments are not a sine qua non for science to be beyond hope. But I remain dissappointed how many really good, top name scientists cling to this view.
You raise a good point on time for science to advance – I agree we have to find ways to hold our feet to the fire and improve on shorter time scales. But especially when I hear people expecting a field established (in some ways) in the 1980s to already have moved beyond pattern, I think we’re being excessively optimistic (arrogant?) about the power and rate of scientific advance. We shouldn’t fool ourselves that publishing thousands of paapers a year in ecology equates to truly revolutionary advances every year.
I hope more macroecologists but also more ecologists open up to microcosms. Ask me sometime about my experience with a Canadian CFI grant to do macroecological microcosm experiments. Suffice to say it never got funded.
As already clear, no disrespect to microcosms. But you’ll have to put me down as unconvinced about microcosm experiments being able to weigh in on the role of productivity and the latitudinal gradient – I think the productivity-diversity relationship is heavily scale dependent as to which processes are most important across the scales. Its not even clear right now that the pattern is the same across scales. I quite agree that historical contingency could be tested with microcosms though. In a way that is what Jon Chase has done (though whether you would count a cattle tank as a microcosm I dont’ know)(and I think Drake did some stuff before).
And just to jump the threads a little – in response to your & Jim’s comments on Platt – Platt worked really well for moleclular cellular biology up to a point – its gotten them to a really long list of important proteins/genes and a mechanistic understanding of how they work, but no real ability to assemble the story into a coherent predictive whole. For all its shortcomings, this is the reason that systems biology is hot right now. I don’t see Platt having a big role in systems biology.
You wrote a CFI to do microcosms (for non-Canadian readers: that’s basically a grant to purchase expensive pieces of equipment)?! Like, protist microcosms? Or something more like Graham and Andy’s stuff? I’m not sure whether I should be embarrassed that I didn’t think of trying that, given that I’m a microcosm guy and you’re not, or glad that I never thought of it and so didn’t waste time getting shot down. 😉 For what it’s worth, I wasn’t one of the reviewers…
Also worth noting that, when I applied for my postdoc at Silwood and John Lawton asked me what I wanted to do if hired, I said “macroecology in microcosms”. My one vaguely-macroecological paper (using microcosm data to look at the local-regional richness relationship) was in the works at the time, I was intrigued by Jim’s and Brian’s books and reading lots of stuff by John and Kevin Gaston and Tim Blackburn…But by the time I actually started the position, I’d changed my mind. Mostly because I’d seen the Phil Warren was already doing work along these lines, but also because my interests had shifted. I’d be very curious to hear what sort of experiments you had in mind, if you were willing to share them over a beer at ESA or something. As I said, back in the late 90s and early oughts I kind of felt like Phil had picked all the low-hanging fruit in this area, but I’ll admit I never really thought hard about what it might be possible to do.
Yes, you certainly can test for historical contingency in microcosms, that’s been a very common use of microcosm and mesocosm experiments, and not just by Jon Chase and Jim Drake. Basically, colonization order is one of the easiest things to manipulate in microcosms and mesocosms, so lots of experiments on that have been done. Now, most of that stuff hasn’t been linked up to ideas about macro-scale consequences of historical contingency, and I don’t know the macroecology literature well enough to know what sort of linkages could be made. From my perspective as a process-oriented community ecologist, I think the frontier for historical contingency research is testing a priori hypotheses about the circumstances in which you expect, or don’t expect, historical contingency. My former labmate Zac Long has done some work on that, and Jon Chase has done a bit too. The other recent trend here is people looking for “long term transients” as distinct from alternate stable states (I’ve even seen people talking about “alternate transient states!”). I have to say that I’m not high on that stuff, even though some of my good friends are doing it. The farther you start a system from its attractor, the longer it will take to return to that attractor; that’s pretty trivial. I haven’t yet seen any papers that convincingly demonstrate some sort of non-trivial, interesting long-term transient (I think it can be done, but it’s difficult). Existing work on long-term transients just strikes me as an (unintentional) way of taking what used to be a criticism of work like Drake’s (how do you know you really have alternate stable states rather than just lengthy transients?) and declaring it to be a feature rather than a bug.
Fair enough if you’re not convinced by Peter’s old “latitudinal diversity gradient in microcosms” idea. Like I said, I don’t remember it well enough to have an opinion, I just remember that it really split the reviewers. I think Peter and Henry Stevens did eventually do a pilot version, didn’t get very interesting results, and so decided not to pursue it further.
Yes, agree that Platt’s ideas aren’t really helpful for contemporary systems biology. Used to be in molecular biology that, if you needed to do stats to tell if your experimental treatment had an effect, it meant you’d done the experiment badly. Now, not only do you need to do stats, you need to get statisticians to invent whole new statistical approaches! 😉
One further thought Brian: If most large-scale macroecological patterns are indeed driven by processes like speciation which are impossible to manipulate experimentally, why is that? That is, how come the fast processes of contemporary population and community dynamics don’t erase the signal of those much slower processes? Because they certainly could. I asked this question in an old post (http://oikosjournal.wordpress.com/2011/05/02/why-doesnt-community-ecology-erase-the-signal-of-historical-biogeography/) and never got any comments. I’d love to have some.
You’re putting up lots of great stuff lately.
“It’s an effective response to anyone who would claim that, if you’re not doing manipulative experiments, you can’t possibly be doing science.”
I find that, for those who hold that view, you’re not likely to convince them of anything, because they almost certainly are not going to understand the importance of simulation modeling in developing theory, the integration and testing of that theory with both simulated and actual data, etc. If they did, they wouldn’t make such stupid statements.
But then, I’m embarrassed to say that I once thought Platt’s (1964) Science paper “Strong Inference” was the be-all and end-all of the discussion on how to make progress in science. Of course, I was working in molecular biology at the time, and that’s basically what their viewpoint is.
Re: the effectiveness of the astronomy analogy as a response to attacks on the possibility of observational science, I meant that it’s an effective response in that it *should* be taken as convincing, not that those making those attacks *actually* find it convincing. But as you say, that’s their problem, not macroecologists’ problem. You can lead the horse to water, but you can’t make it drink.
Re: Platt, I think this gets back to Florian’s remark about how every field faces its own challenges. In molecular biology, “strong inference” really is an effective way to solve the sorts of challenges molecular biologists face. And as I’ve noted in other posts, I actually do think “strong inference” could be more widely used in ecology than it is. But no, it’s not the be-all and end-all of how to make scientific progress.
I think that Brian has already said everything I would have said, and far more eloquently at that. So +inf to Brian’s comments. I think they do a great job of clarifying how macroecologists think about this sort of thing.
You’re not getting off that easily! Next I’m going to do a post comparing macroecology to some other random scientific field, and it’s your turn to comment first.
“Is macroecology like inorganic chemistry?”
“Is macroecology like psychology?”
“Is macroecology like Asian studies?”
So many possibilities…You’d better start your background research. 😉
“Next I’m going to do a post comparing macroecology to some other random scientific field”
A comparison to “microecology” might be a good one, assuming we can define these well enough to compare them.
Implicitly, that’s basically what most of my previous posts on macroecology do.
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I found randomly this very interesting thread; great post and comments (will these ideas ever reach general ecology textbooks?). I’m really happy to read this, as I often use the comparison to astronomy to justify the observational method in ecology. So I add a few comments – constructive I hope.
There is no doubt we can do experiments at times, but I would point out it really depends on the taxa you’re working with – for large animals or long-lived trees, experiments are rarely practical! Sometimes textbooks will put e.g. interactions between wolves and moose in boreal forests alongside interactions between zoo and phytoplankton in the lab, however it is very unclear how much we learn on the role of predation in structuring vertebrate communities by comparing them to plantkon in an aquarium. We certainly learn from microcosms but by definition we study small species, thus we need observational data to check findings hold for larger species on which we can’t experiment.
With respect to point 2), I think the well-validated theory you refer is not astronomy/astrophysics as a whole, but the theory of planetary motion + the study of star composition… It seems that at large-spatial scales (clusters of galaxies and above), much mysteries remain (great special issue of Science on this http://www.sciencemag.org/content/336/6085.toc#SpecialIssue) – the theory is in development as in ecology. Most of the matter of the universe is still “missing” with several competing theories for this. It seems however physicists are very organized in their attempts at connecting the theory to data (sharing telescope time, etc.), from an outsider’s perspective at least, while in ecology, research might often be more “individual-centered”. Anyway, the quality of the theory really depends on what specific subject one is looking at…
As to point 3, not only large-scale patterns in the distribution of matter are key to cosmology (I rejoin Florian here), but current research on exoplanets seems also devoted to finding large-scale statistical patterns (at least, the part that lands in the pages of Nature or Science http://www.nature.com/nature/journal/vaop/ncurrent/full/nature11121.html, http://www.nature.com/nature/journal/v481/n7380/full/nature10684.html). Historically, spatial point process models to study the distribution of plants or animal nests have also been used to study the spatial clustering of galaxies (e.g. the Neyman-Scott point process). Knowing whether the approaches have been equally popular in both fields, I reckon, would require the expertise of an astronomer!
So I would say the analogy can work quite well depending on your subfield. From my perspective, it applies also well to population/community ecology. I am working currently on population cycles in small mammals, which requires (primarily) long-term observational data on predator-prey communities. Despite that, I still read quite often that we will not know for sure what causes declines for a given species/place until we perform experiments removing predators (which is quite debatable – given any such “experiment” modifies countless other things). Researchers are sometimes close to apologize for not doing experiments. In this particular case, I’ve got two guesses for the appeal of experiments: on the one hand, we have very poor observational data on several important predators, and on the other hand, mathematical models are often weakly related to data or their assumptions misunderstood.
These problems in population ecology, combined to the discussion so far suggests to me two quick thoughts:
1 – Training may have an impact on the “respectability” of various approaches. In ecology, most researchers are arguably biology majors, and what is taught at undergrad level is physiology, molecular biology, etc.: disciplines that emphasize the experimental approach. This probably has an impact on all of us. Then most of the statistics we learn – thus the statistics most researchers know how to do without engaging in a mathematics battle – are designed to analyze controlled experiments; again, the experimental approach. The example of evolution as an observational discovery is interesting: though many ecologists are naturalists, much of the training at university in biology goes in a completely different, experimental direction. If the training was instead a combination of natural history and applied mathematics, I bet the number of extreme fans of the experimental approach would decrease quite a lot. This brings us to a difference with astronomy / astrophysics, this time: you can’t enter graduate studies in these fields out of love for the stars and without a strong quantitative background. In ecology however, many students are recruited with a maths-free and pro-experiment undergrad degree in general biology, and this itself might contribute to generate a strong experimental tradition.
2 – Observational tools are a crucial element of astronomy and have paralleled its long maturation – maybe in ecology we are still missing crucial observational tools. I’ve peered through a rather interesting book on exoplanet hunting (http://press.princeton.edu/titles/9404.html), and much of it is devoted to the description of the new tools that allowed to discover planets orbiting stars – before that, this field of research was closed. As the saying goes, “plants stand still and wait to be counted” (though plant ecologists might disagree!), but for animals efficient monitoring tools are often lacking. To use a concrete example, to monitor the effects of vertebrate predators on their prey, a few decades ago it was easier to keep lynxes (or other charismatic top consumer) out of an exclosure rather than monitoring the movements/kills of a sizeable fraction of the population. Now, the reverse is probably true – so the interest of experiments clearly depends on the technology that records observations. In behavioural and population ecology, modern techniques such as GPS and other biologgers, arrays of cameras and microphones, photo or genetic identification, etc., are opening the door to better, more detailed observational studies. (+remote sensing for macroecology?)
To sum up my points, lack of quantitative training to analyze observational data, and lack of proper tools to record enough observational data might tip the balance in favor of an experiment-only philosophy in some fields. Otherwise the astronomy analogy sounds pretty good to me (but clearly that depends on what species/groups you’re working with)!
Very good comments Fred, thank you.
Re: the ability to extrapolate results from one system to another, the answer of course is that sometimes you can and sometimes you can’t. I have an old post which touches on this issue, noting for instance that the average strength of “trophic cascades” in protist microcosms in the lab is almost frighteningly similar to the average strength of trophic cascades in nature.
Yes, you and others are right to note that astronomy is not a homogeneous field. Some subfields of astronomy seem more analogous to macroecology than others. I think this is an important point. Even after one grants that “observational” science can still be good science, there are still many questions as to what kinds of observations you need, and what kinds of other things (like mathematical theories) you need in order to make progress on whatever question you’re asking.
Yes, if we trained our students differently, they would surely “grow up” to have different attitudes about experiments, or mathematics, or etc. Unfortunately, this is somewhat easier said than done. It’s more difficult to train your students in something you don’t know well yourself. And students also choose what sort of training they receive, for instance by choosing their supervisors. Most students who go into ecology do so because they love nature, or some particular bit of nature (birds, say, or mountain habitats, or whatever). They don’t go into ecology because they love math (indeed, often just the opposite!).
Good point about improvements in our observations opening up new avenues for scientific progress. You’re certainly correct that much of the history of astronomy is of progress (in terms of both what questions we can ask, as well as the precision of our answers) has been driven by improved instrumentation (measuring more things, and more kinds of things, more precisely).
Thanks for the link, I was just reading about trophic cascades… it opens perspectives.
I would not be so gloomy about quantitative training, things are changing – for instance, half the postdocs I see advertised today are strongly quantitative, at some point this will reflect on the training. Many postgrads I talk to use R, do complicated stats, and are sometimes quite bitter to have discovered after years of studies that they actually need maths and programming on a daily basis – especially when they’ve been told otherwise! I may be naive there, but it seems quite feasible to at least advertise early on the quantitative nature of ecology.
The difference with astronomy might not be that students love maths there (I would not be so sure most physicists “love” maths), but that physicists agreed on what the students have to know to graduate in their specialty.
Though again, it would be interesting to have a physicist perspective on these issues.
By the way, we will soon present the results of that “maths and ecology” survey (with INNGE) that you relayed on the blog a while ago.
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With the caveat that my knowledge of astronomy is pretty poor…
It seems that the key difference is that astronomy is fundamentally the study of a few discrete objects interacting with each other. The rotation of planets around the sun, gravitational interactions between large, essentially discrete masses, etc. I think that the more objects you have to deal with, the more difficult it is to work with exactly. In that sense, macroecology is more like macroeconomics: a fundamentally statistical venture.
But I could be totally wrong 😉
Yes, that’s more or less what I argued in the post. As other commenters note, that argument works for certain branches of astronomy, but not others.
Oof, not my day, somehow I missed that when reading/(only a little skimming, I promise!)…I should probably read more carefully…
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