Many ecologists, including me, want to discover generalities. We want to see the forest for the trees. That often means abstracting away from certain details so as to focus on features shared by all cases of interest.
But is there such a thing as too much generality, or the wrong kind of generality? It’s a good thing to step back and see the forest for the trees, but what if you step back too far (into deep space, say)? Don’t you lose sight of the forest, or end up mistaking the forest for something else?
I think so. In seminars, I sometimes use the hypothetical example of a ‘general theory of growth’. Try to imagine a general theory of growth that would apply to everything that can be said to ‘grow’. Not just individual organisms, but populations, economies, egos, the entire universe…The point is that just because two things can both be said to ‘grow’ doesn’t mean they’re comparable in any interesting or useful sense. Note that one could statistically compare the growth rates of, say, organisms and egos. But that doesn’t make the comparison scientifically meaningful. I use this example because it’s obviously silly–at least, I thought it was obviously silly. Then I attended a philosophy seminar at which the speaker argued, in all seriousness, that major disciplinary boundaries (e.g., between astronomy and biology) inhibit scientific progress because they inhibit the development of general theories–such as a general theory of growth that might apply to everything from growing organisms to the expanding universe. So at least to some, there’s no such thing as too much generality!
Moving away from hypothetical examples and the sort of philosophers who focus exclusively on them, there are real-world examples of overly-general theories or concepts in ecology and evolution. The obvious examples are theories which were empirically false due to their over-generality. An example is the pre-Darwinian idea that development of individual organisms and evolution of species are closely analogous. Darwin showed that that’s just false–development is directed towards a pre-determined goal, evolution isn’t. So the notion of ‘development’ doesn’t apply nearly as generally as some pre-Darwinians thought.
But more interesting cases are when theories or concepts are over-general without necessarily being empirically false. Over-generality in this sense is trickier to pin down, but can involve such features as:
- vaguely-defined terms
- loose analogies
- lack of a general mathematical version of the theory or concept. Thereby forcing reliance either on purely verbal models, or else on less-general mathematical models of specific cases, from which over-general conclusions are drawn
- reliance on purely statistical tools to compare and contrast different case studies in a phenomenological way (as in statistical comparison of the growth rates of organisms and egos)
All these features have the effect of facilitating comparisons of ‘apples to oranges’–comparisons that highlight comparatively superficial commonalities among different cases, while obscuring deeper distinctions that need to be drawn in order for explanatory progress to be made.
I’ve argued that the idea of ‘biodiversity affecting ecosystem function’ (BDEF) is over-general in this way (Fox 2006, Fox and Harpole 2008). The terms ‘biodiversity’ and ‘ecosystem function’ are like the term ‘growth’–they embrace many phenomena which really need to be kept separate in order for explanatory progress to be made. I have used the Price Equation to suggest what distinctions ought to be drawn between different classes of BDEF problems (a ‘divide and conquer’ approach, if you like). This formal mathematical approach forces precise definition of terms, and highlights not only important distinctions but also important but unrecognized commonalities. For instance, ‘community variability’ is not generally regarded as an ‘ecosystem function’, but effects of biodiversity on community variability can be analyzed within the Price Equation framework (Fox 2010).
One very prominent ecological idea which has been criticized as over-general is a citation classic: Jones et al. (1994), ‘Organisms as ecosystem engineers’ (>2100 WoS citations). Jones et al. define ecosystem engineers as “Organisms that directly or indirectly modulate the availability of resources [other than themselves] to other species, by causing physical state changes in biotic or abiotic materials. In so doing, they modify, maintain and create habitats.” The concept has subsequently been broadened to include essentially any effect of organisms on their physical environment (e.g., Harmon et al. 2009). Ecologists now have a huge range of case studies of ecosystem engineering (reviewed in Wright and Jones 2006), mathematical models of a few specific examples (e.g., Wright et al. 2004), and an admirable attempt to unify these disparate examples within a general (but unfortunately, not fully specified) mathematical framework (Jones et al. 2010). Despite all this, even ecosystem engineering’s staunchest advocates recognize that they have yet to present a fully-convincing argument that they’re not comparing apples to oranges (Jones et al. 2010). That some specific models of ecosystem engineering (e.g., Wright et al. 2004), and some prominent case studies (e.g., Harmon et al. 2009) appear not to fit within the general mathematical framework of Jones et al. 2010 is a little worrisome. I honestly admire the imagination and ambition of the idea of ecosystem engineering–big ideas like these can drive real progress in science. But I remain to be convinced that there is a general, non-trivial theory that covers everything from the creation of aquatic habitat by beavers (Wright et al. 2004) to the effects of stickleback fish on the chemical composition of DOC (Harmon et al. 2009).*
None of which is a criticism of anyone whose worked on BDEF, ecosystem engineering, or other ideas that may be overbroad. Probably, if we’re not overgeneralizing sometimes, we’re not trying hard enough to generalize in the first place.
*And based on a quick glance at citation data, I wonder if the field as a whole is starting to agree with me. Jones et al. 1994 has only been cited 165 times this nearly-completed year, way down from 211 last year. And before this year, citations of Jones et al. 2002 had been essentially flat since 2012 (203-215 citations annually). Which means that citations of Jones et al. 2002 have effectively been declining since 2012, given the rapid exponential growth of total citations. Of course, there are lots of reasons why interest in ecosystem engineering might be starting to decline. So I’m being a facetious in suggesting the whole field agrees with me that ecosystem engineering is an overbroad concept.🙂
Note: this is a lightly-edited rerun of a post that first ran on the Oikos blog back on May 11, 2011.