How to revolutionize a scientific field in five not-so-easy steps

Just finished reading this very interesting 1971 address to the American Economics Association by Harry Johnson. He asks what determined the speed of the Keynesian revolution in economics, and the monetarist counter-revolution. In it, he suggests that a revolutionary theory has the following five characteristics:

  1. It has to attack–and ideally reverse–the central theoretical proposition of the prevailing orthodoxy. Ideally, the motivation for the attack should the inability of orthodox theory to explain some important empirical data.
  2. It has to be new, but yet also incorporate as much as possible of the less-disputable bits of the prevailing orthodoxy. Pulling off this apparently-contradictory trick generally requires putting old wine in new bottles: renaming established concepts without admitting that you’re doing so. It also can involves shifts in emphasis, for instance by emphasizing the importance and non-obviousness of points that were previously considered unimportant and obvious.
  3. It has to be too difficult for senior people to bother to understand, and somewhat-difficult-but-not-too-difficult for junior people to master. This gives junior people a way to work around the conservatism of senior leaders in the field, a reward for doing so, and a sense of belonging to a shared intellectual project.
  4. It has to offer some low-hanging fruit, especially to empirically-oriented researchers (as opposed to theoreticians). Ideally, it will give the junior people who master it a straightforward, “crank the handle” methodology for producing publications.
  5. It has to pick out a new, measurable empirical pattern or relationship. A stylized fact that empiricists can target for further investigation. This goes hand in hand with #4.

This story seems to fit the potted history of 20th century macroeconomics pretty well, though of course I’m no expert. So here’s my question: does it fit any revolutions in ecology? And does lack of any of the 5 attributes on this little list explain the failure of any attempted revolutions in ecology?

Just off the top of my head, I’m not sure ecology has had any revolutions that fit this scheme perfectly. Maybe that’s because, to have a revolution, there has to be an orthodoxy to revolt against? Can a scientific field in which there is no prevailing orthodoxy, or that arguably isn’t even a single discipline at all, be revolutionized?

The MacArthurian revolution starting in the late ’50s does seem like it fits some of the items on this list (see also). I’d say it fit #3-5 fairly well, and arguably #2 as well. Not so sure about #1 though.

The counter-revolution against (what was taken to be) the MacArthurian view in the late ’70s and early ’80s (the “null model wars” et al.) definitely fit #1 and I suppose arguably fit #3-4. Not sure about the others.

The attempted revolution of Hubbell’s neutral theory definitely  appeared to have #1, 2, 4, and 5. (Aside: neutral theory is a great case study for how an idea can take off in part by being widely misunderstood). Not sure about #3 though. And the revolution failed once everybody realized that it didn’t actually have #1 and #4.

What do you think? Have there been revolutions in ecology, and if so, have they fit this 5-part template? Looking forward to your comments, as always.

9 thoughts on “How to revolutionize a scientific field in five not-so-easy steps

  1. I don’t think # 3 is necessary at all ; Sr people are often so wedded to the old ideas that’ difficulty in understanding’ is not a barrier to them. The barriers lie elsewhere. And jr people are almost always open to new ldeas .. those with obivious promise.

    So I nominate the ESS revolution in behavioral Ecology as meeting all the other criteria.

    • Do you think the ESS revolution satisfied #1? If so, what was the dominant orthodoxy it reversed? Or was ESS an example of a revolution that wasn’t in revolt against a dominant orthodoxy?

      • Yes, it satisfied # 1. In one sense it was the very careful use of individual natural selection to produce much deeper adaptational explanations for all sorts of STUFF. Many very facile adaptational explanations , most species level benefit, existed for all sorts of stuff; eg, Anisogamy, alarm calls, communication, habitat selection,sexual behavior & structure, etc…..and they were rapidly replaced by much better ideas.
        My favorite was the invasion of ESS ideas into plant reproductive ecology, particularly with sex allocation, male reproductive success, and selfing avoidance/regulation. Imagine thinking about pollination systems mostly in terms of female reproductive success [ outcrossed seeds produced], and not considering male reproductive success as an equivalent fitness gain path in hermaphroditic plants; that was the world before the mid to late 1970s. And even selfing avoidance/regulation was recast in individual/genic level benefit, having drifted into a species level benefit for decades before.
        I attended an international conference on reproduction in higher plants in New Zealand in the winter of 1979, and except for me, David Lloyd, James Beach, Dan Lewis, and Kamil Bawa, the papers were group level benefit, or mostly descriptive in subject. The revolution had just begun.

  2. I think I broadly agree that #3 is not quite-right. Some of this is that it is saying something very similar to #4 in that one should provide sufficient motivation for junior people to help build an idea out to its fullest extent, and also that difficulty is not the proper metric to disincentivize senior people (at least this is my impression). Perhaps another way to put it would be to say that 3a). Senior people should be disincentivized from arguing with the theory (either they are uninterested in it, or it isn’t personally threatening to them in some way that they feel they need to attack it earnestly, or something else), and 4a). younger people should be encouraged to get involved and make progress developing the theory, so that they have some personal stake in its successes.

    Anyway, this is quite an interesting list just to consider. Because of your blog I’m now far more familiar with Lakatosian thinking regarding science, and this seems like a nice “application” of this perspective in a way. Personally I’m hoping to try and accomplish just half of this in the field of pattern formation – namely, demonstrate that the current approaches really are insufficient, and their successes are overstated. Unfortunately I don’t yet have a solid alternative that can easily be shown to be better, and so this task may be futile as people rarely leave a sinking ship unless there’s some other boat they can swim towards (cf. string theory).

  3. Interesting conjecture. What works in an inherently politicised discipline like economics may not always work elsewhere. More to the point for me, though: has anyone written a history of ecology recently? I suspect most graduates, like me, would have little clue as to what actually happened in the history of ecology.
    (sorry for coming to this blog post so late)

    • “has anyone written a history of ecology recently? ”

      Sure. There’s Sharon Kingsland’s Evolution of American Ecology 1890-2000, and further back her excellent Modeling Nature. There’s Nancy Slack’s G. Evelyn Hutchinson and the Invention of Modern Ecology. Maybe others I’m forgetting just now.

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