The best thing you’ll read about ecology this week was written in 1975. It’s Stephen Fretwell’s reflections on the influence of Robert MacArthur, published in Annual Review of Ecology and Systematics (as it was then known) three years after MacArthur’s death from cancer aged just 42. Embarrassingly, I was unaware of it until a correspondent brought it to my attention.
MacArthur was the rare scientist who (along with his collaborators) changed the direction of an entire field. Many ecologists doing basic research today are still following in MacArthur’s footsteps, or else reacting against him (consciously or not). So if you want to understand why ecology is the way it is, you need to understand how it used to be, and how MacArthur changed it. It’s a fascinating historical case study with implications for issues both contemporary and timeless. Fretwell’s piece touches on everything from the role of hypotheses in science, to the role of elite scientists and peer review in scientific publishing, to the connections between one’s professional and personal life.
Below the fold are a bunch of extended quotes from Fretwell (1975), along with some comments, to give you the flavor and encourage you to read the whole thing.
MacArthur as introducing the hypothetico-deductive method into ecology:
This method [the hypothetico-deductive method] has had great success in many fields of science (physics, chemistry). But, prior to MacArthur’s 1957 paper on relative abundance, it had been little used in the study of natural history (about 5% of papers in Ecology from 1950-1956 tested predictions, compared to almost 50% nowadays). MacArthur accomplished two things with respect to furthering the use of this method: he provided acceptable examples of how one should do H-D science and he provided leadership and protection to those who wanted to work this way.
The prevalence of hypothesis-testing research is still increasing in ecology journals. To the point where some would argue that ecologists now place too much emphasis on hypothesis testing, at least when the hypotheses are statistical null hypotheses rather than substantive scientific hypotheses.
On the hypothetico-deductive method, the opposition of research and “scholarship”, and the role of authority figures in science:
The issues were (and still, in part, are) these: Should scientists be allowed to make mistakes in print? How extensive is one’s responsibility to previous literature and scholarship? The first issue is usually precipitated by so called “weak” tests of theories. These are insubstantial data contributions in response to a theoretical prediction, confirming the prediction but only raising the plausibility of the theory a modest amount. Critics claim that such “tests” mislead the naive into believing that the theory is proved. One hears that science reaches “conclusions,” i.e. ideas are proved correct, and that then (and only then) should work be published. The second issue pertains to rejection of clever or interesting statements because they are not interpreted in light of most of the previously published reports that seem related.
MacArthur never really discussed these issues; he just took a position. The position he took was intellectually sound, but socially risky. He simply went ahead making and publishing predictions and weak tests of predictions…Nor did he overwhelm possible critics, or play citation politics, by including “all the right” references. The rest of us did not have to wait until an endless debate on scholarly principles was settled before we dared to seriously consider using weak data to test loosely formulated models or to discuss a new idea without a lengthy library research. MacArthur was famous enough to silence most criticism and provided an outstanding example of success, doing just what he sensed needed doing to excite himself and his many reasonable colleagues. From a position of authority, he ignored, and so took responsibility for our ignoring, the reviewer of research who looks for and at mistakes instead of assessing progress. Thus his contribution to the people who let themselves be positively affected by him was both to point the way for a radically different perspective on how ecologists should proceed and to get famous enough so that we could follow this direction without undue harassment.
Fretwell’s comments here are very interesting. He almost sees the inconclusiveness of MacArthur’s data as a virtue rather than a vice. Fretwell is all in favor of hypothetico-deductivism, but worries that premature tests of hypotheses can strangle good ideas in the cradle. For him, the “riskiness” of hypothetico-deductive science is in daring to make a prediction in the first place, not in testing the prediction. As Fretwell makes clear in other passages, he thinks it’s much more important for hypotheses to be interesting than to be right. Or at least, he thinks that the rightness of hypotheses should only be evaluated after many studies have been conducted; one shouldn’t worry what the initial data suggest. He’d probably be distressed to hear that today many ecologists think (or think other ecologists think) that any new hypothesis proposed in a general ecology journal should be accompanied by a rigorous test, and that the most cited ecology papers these days are methodological and applied papers rather than papers proposing new fundamental hypotheses.
Conversely, Fretwell’s not worried about hypotheses getting established prematurely. I think he should’ve worried more. More than one zombie idea in ecology established itself in more or less the MacArthurian way: an interesting idea was proposed but not developed very rigorously, with a bit of merely-suggestive data presented in support. Contra Fretwell, I don’t think the “but in MY lake” school of ecology has provided much inoculation against zombie ideas.
Particularly curious to hear Brian’s reaction to Fretwell’s remarks on hypothetico-deductivism. On the one hand, Brian’s on record bemoaning the lack of big new ideas and bold hypotheses in ecology. On the other hand, Brian’s bothered by ecologists’ collective lack of a problem-solving mentality: we don’t ever permanently reject many of those big ideas. Don’t worry, I’m not trying to catch Brian in a contradiction here, or set up a straw man Brian and then force Brian himself to knock it over. I just want to better understand Brian’s thinking on the balance (trade-off?) between creative hypothesis development and rigorous hypothesis testing.
Also interesting is Fretwell’s view that it’s actually a good thing for someone to be so scientifically famous as to be mostly above criticism. That’s not a view one hears much in contemporary debates about scientific publishing! That just goes to show that authority figures, like most things, aren’t inherently good or bad for science. They can aid or hinder the progress of science, depending on the circumstances.
We should publish ideas reviewers don’t like; that’s what PNAS is for:
Not all wrong ideas are innovative, of course, but all truly innovative contributions must, on first reading, appear wrong. Scientific papers should never be rejected because someone is found who disagrees with the ideas presented. Quite the contrary, a truly scientific journal might reject as unnecessary any paper that failed to elicit such criticism…The National Academy of Sciences (NAS) once had the enlightened view that any idea that impressed one intelligent scientist (i.e. a NAS member) was worthy of publication. Many of MacArthur’s significant ideas were expressed in the journal of that society (the Proceedings of the NAS) with Hutchinson’s blessing. Having bypassed the normal review process, he was well on his way to becoming famous.
Bibliometric analyses of PNAS papers are consistent with the notion that PNAS allows NAS members to publish interesting but unconventional ideas. I’m curious what Fretwell would think of innovations like preprints, blogs, and journals that evaluate manuscripts only on technical soundness. On the one hand, I think he’d like that it’s now easier to publish interesting science with which many scientists would disagree. On the other hand, I think he’d dislike that it’s now easier to publish boring science that nobody disagrees with because nobody cares about it.
You shouldn’t read or cite the literature too much:
The process of prediction making requires such strict logic that peripheral references merely distract…Few scientists realize how antithetic are scholarship and science…Consistent with his use of H-D science, MacArthur rarely used a broad literature base in his work.
I agree with Fretwell here. There’s such a thing as immersing oneself in the existing literature too much, or taking it too seriously. For instance, the reason I was able to write a cogent critique of the intermediate disturbance hypothesis is precisely because I don’t work on it and don’t know the literature on it all that well.
MacArthur as a “temperate revolutionary”:
MacArthur’s position towards “the establishment,” i.e. authority, and leadership in science was enlightening. He clearly trusted and respected the system and was hopeful that, with proper leadership, it could be made more effective in accomplishing science. Although he did things differently, he did try to move so that the system was not offended. So, he succeeded in having an impact. Insofar as optimism can be cultivated or passed on, his effect on what might be called “revolution” in ecological method was therefore a temperate one.
As someone who basically trusts and respects the system—including the ability of the system to change with the times—this really resonated with me. Innovation and conservatism need to be balanced.
A test of a good ecologist:
He [MacArthur] later told G. Lark (personal communication) that a good test for an ecologist was to walk with the person through a field and see how many questions he asked.
I suspect I would fail this test, so I’m glad that Fretwell goes on to say that he doesn’t think this test should stand alone.
On the role of family life in one’s scientific life:
When I knew him (in 1968-1969) he was above all a family man; he spent much time at home, and he surely loved his wife and placed her first. This is, admittedly, a personal question, yet, it is one that must pervade every scientist’s life: to marry or not, and, if married, how much of one’s time that could be spent in research should be spent instead with one’s family…I had the distinct impression that MacArthur worked on ecology mostly when his family got tired of his hanging around. I suspect that he had the freedom to do what he did for ecology, going against all convention, because it was all secondary to him anyway; or maybe he just spent so much time with his family that he never really had time to learn the conventions! Yet, even so, look at what he accomplished! One can argue (I often do) that it was his genius that allowed him to so lightly toss off pieces of research and so to be home more. However, I am dissatisfied with this interpretation…Just as plausibly and much more usefully, I now believe that MacArthur’s personal priorities (family before profession) were part of what made him so successful. For, in inspecting his work, the freedom is more conspicuous and more unique than the brilliance; the freedom, then, is the major contribution. And such freedom very cogently follows from lowering research and publication into a second (or lower) place.
These remarks need to be read in the context of their time. But I don’t think they’re totally out of date. In particular, the notion that MacArthur was successful in part because he didn’t care too much what others thought is a generalizable lesson, I think. You can’t stand out from the crowd by just following the crowd, and you need to play to your own strengths. I’d like to think I’m pretty good at that. I’m hardly on MacArthur’s level as a scientist, of course! But had I followed the conventions of ecology too closely, or worried too much what other ecologists would think of me, I wouldn’t be working in microcosms, and I wouldn’t be a blogger. Both of those unconventional choices have worked out very well for me. And the message that you can succeed in science without having to work crazy hours, even if you’re not “brilliant”, remains timely and true.