Ecology is infamously variable. Every individual organism, site, time, species, population, community, ecosystem, landscape, [your favorite ecological thingy] differs from others in some respects. So how do you achieve generality? How do you discover (or impose!) some sort of unity, order, law, commonality, [your favorite synonym for ‘generality’] in the face of polyglot variety?

I can think of five roads to generality in ecology:

**Meta-analysis/statistical description.**I think of this as the Jessica Gurevitch approach, since she pioneered meta-analysis in ecology. Or maybe the NCEAS approach. Both the strength and main weakness of seeking generality via statistical summaries is that you can statistically summarize*anything*. So you need to make sure you have some good independent reason for lumping together whatever it is you’re lumping together, so that you’re not lumping together apples and oranges. If you think that’s a trivially obvious point, well, it’s not. There are*many*categories that*lots*of ecologists study that arguably are the equivalent of lumping together apples and oranges. See this old post for more on the challenges of deciding which things are*relevantly*similar to which other things, so that it makes sense to, say, calculate the average value of some property of those things.**Focus on one or two key processes.**I think of this as the Robert MacArthur approach, though you could identify it with many other practitioners (Lotka, Volterra, Levins, May…). You develop a “strategic” or “toy” model that describes some process or factor in a simple way, and make the simplest possible assumptions about other processes or factors. You then hope that your model applies in an approximate way to a wide range of systems–that it “captures the essence” of what’s going on in some general class of cases. This approach has it’s share of successes, most notably island biogeography theory. Arguably also the metabolic theory of ecology, depending on how exactly you define that theory and how successful you think it’s been (see here and here). And other successes too. But I’ve come to think that this approach may have had its day in terms of empirical success in ecology, and remains useful more as a conceptual tool. A way to test and correct one’s pre-theoretical intuitions (which is a*hugely*important task!), rather than a tool to make even rough predictions about how nature generally will behave. I say that because of my admittedly-vague sense that most phenomena of interest in ecology aren’t driven primarily by one or two factors, with others being of at most minor importance. And also because I think testing toy models well is quite difficult, while testing them poorly is dangerously easy. But I could well be wrong. Maybe we just need to a better job of training ecologists to spot systems or situations in which a toy model is likely to make reasonably good predictions even though lots of other factors would seem to be at play.***Look for “statistical attractors”.**I think of this as the Steven Frank approach, but to most ecologists it’s more familiar as the macroecology approach, or lately the MaxEnt approach. It’s basically the opposite of the previous approach. If whatever you’re studying represents the aggregate or “high level” outcome of a large number of underlying “low level” events, processes, or factors, no one of which dominates the others, then this is the approach for you. The high level outcome is a “statistical attractor” (Steven Frank’s term) that’s commonly observed because only a very unusual combination of lower-level events, processes, or factors could produce any other outcome. Think of how the normal distribution arises in a wide range of circumstances, thanks to the central limit theorem. The main problem with this approach arise when investigators forget why it works. Remember: if the “high-level” outcome exists because many different combinations of “low-level” processes or events lead to that outcome, then you*cannot*use the high-level outcome to infer*which*low-level processes or events actually produced the outcome. Put another way, macroecology is community ecology all the way down–even if you can’t infer anything about community ecology from macroecology.**Develop a theoretical umbrella that unifies and subsumes various special cases.**I think of this as the George Price approach, or the Peter Chesson approach (or the other Steven Frank approach). For instance, Peter Chesson’s work on coexistence mechanisms is sometimes misunderstood as being based on one or two specific models. In fact, Chesson’s results apply to an extremely broad*class*of models–*any*model that has certain common properties (see Chesson 1994). He’s proven that all models in the class can exhibit only a small number of different kinds of coexistence mechanisms (e.g., relative nonlinearity, the storage effect, and fluctuation-independent mechanisms) and shown how to quantify the strength of those different kinds of mechanism. This provides a general framework in which one can compare and contrast different models, and empirical situations described by those models. I think this is an underused approach in ecology. Or maybe it’s used a lot and we just don’t recognize that it’s being used. For instance, “density dependence” just means that per-capita growth rate depends on population density–which it might for all sorts of mechanistic reasons, some of them quite indirect. We unify and subsume all of those different mechanisms under the umbrella of “density-dependence”.**Identify analogies between cases that are otherwise distinct.**I think of this as the Tony Ives approach. For instance, lots of different ecological systems have been hypothesized to exhibit alternate states, with stochastic perturbations occasionally flipping the system from one state to the other. In the linked post, Tony Ives talks about how his previous experience with alternate states in other systems helped him recognize and model the possibility of alternate states in the dynamics of Icelandic midges. Here’s a terrific essay I’ve linked to before, from a mathematician who explains why this road to generality often isn’t recognized as a road to generality at all.- UPDATE:
**Do a distributed experiment.**Thanks to a commenter for reminding me of the NutNet approach. Can’t believe I forgot to mention that! And click through to the comment for several other interesting suggestions on roads to generality in ecology.

And one that’s not so much a road as a wall:

**Give up.**I think of this as the John Lawton non-approach, because he famously argued (probably deliberately provocatively) that community ecology was just a stamp collection of special cases and we should quit doing it. Click through for my response to John, but here’s the short version: he’s mistaking the failure of some community ecologists to take any of the five roads just listed for the absence of roads. In particular, I think John completely misses the possibility of the last two roads as viable roads in community ecology. In fairness to John, I think he’s far from the only scientist to overlook or dismiss certain ways of generalizing and then mistakenly conclude that no generalization is possible (e.g., see this comment of mine).

One interesting question is what determines when one approach is more effective than another. I think it’s fairly clear when approaches #2 and #3 will or won’t work. But I’m not sure when the other approaches will or won’t work. For instance, in my own work I’ve applied the Price equation to a wide range of problems. Most of those applications seem to me (and others) to be quite useful, but even I’m not sure if one of them is useful or not. There are many ways to “collect stamps”, but I don’t think nature gives us a completely free choice as to how to do it.

p.s. I just wanted to say I’m proud of myself for dropping so many famous names in one blog post. 🙂

*In one of my first posts, I referred to this very real and valuable skill–the ability to recognize situations in which a simple model is likely to decently-approximate a much more complicated reality–as “good hand waving”. I used some friends whose work I greatly admire as examples. I meant it as a compliment but I don’t think it came off that way. Both because I wrote the post badly, and because “hand waving” has negative connotations I didn’t intend.

Thanks for another great post.

Five more roads that have perhaps been less-travelled in the search for generality in ecology

6. The global distributed experiment: Design manipulative experiments that extend across the widest possible domain of the phenomenon that you wish to explain. Example NutNet

7. Be persistent: Long-term studies that by the simple virtue of their time-depth can provide insights into what ‘generally’ happens. Example LTERN

8. Embrace complexity: Permit the general to be complex: Example Gurevitch et al. (2011) Emergent insights from the synthesis of conceptual frameworks for biological invasions. Ecology Letters 14: 407-418

9. Crack the issue of scale and learn how to upscale and downscale based on a mechanistic understanding of process.

(and a not recommended approach)

10. Shout about it often enough and people will think it is generally true. (tongue-in-cheek)

6. That’s a great one! I’m embarrassed to have forgotten that, since I’m a big fan of NutNet. I guess you could call it a subspecies of my #1 (it’s just that all the data for the “meta-analysis” comes from one big distributed experiment), but really it’s its own thing.

7. Hmm. I think I see what you mean. But as someone who’s suspicious that space-for-time substitutions actually work all that well, I’m inclined to be suspicious of time-for-space substitutions. But perhaps I’m misunderstanding you on this one?

8. Hmm. Not sure if that counts as a road to generality so much as giving up (while pretending that you’re not giving up). But I haven’t read Gurevitch et al. 2011 so perhaps I’m misunderstanding here.

9. I think that’s possible in tractable model systems, which is one argument for focusing more on model systems.

10. I’ll probably surprise some readers by not touching that one. 🙂

Thanks for your responses. To help clarify a bit further on the items 6-9.

6. Yes I consider the big distributed experiments, such as NutNet and the many like it, to be a very compelling approach to generality. That said, we have a long way to go to really achieve coverage that is representative geographically and across all biomes. But a good start has been made with this new model for collaborative work.

7. I am highly suspicious of space-for-time also, and so I am not recommending a time-for-space either. What I am simply pointing out is that even the things we think we know well can be improved by capturing more of the dynamic over time, and there often a few surprises along the way.

Imagine re-doing a meta-analysis for experimental datasets that were continued beyond the typical 3-year window. Would the results be consistent over time, would the effect sizes for different factors change in qualitative ways?

8. Generality does not have to equate to simplicity, especially in complex ecological systems that are highly connected and exhibit feedbacks. What appears to be the general outcome will shift as we shift our focus. This is probably close to what you outlined in number 4.

9. Yes I agree that working in tractable or model systems helps to generate the general principles at work. Trick is figuring out why they are tractable in the first place and others appear not to be so.

BTW – I recommend many of your posts to my grad students. So thanks again for keeping up the exchange of fresh ideas with the great masses in the blogosphere.

Thanks for the great comments!

Re: why model systems are tractable, we have an old post on this, which you may have seen. The comment thread is one of our best ever; gets into related issues like how many model systems ecology might need:

https://dynamicecology.wordpress.com/2012/10/18/ecologists-should-quit-making-things-hard-for-themselves-and-focus-more-on-model-systems/

A thought provoking post, Jeremy! I especially liked the section concerning stochastic perturbation theory. My lab is considering delving into these approaches, with some subtle alterations- i.e., that “flipping” of the system, at the level of the community, is continuous & simultaneous, and that all alternative states coexist via some sort of flux dynamics.

For those interested in this theory- there is a great paper out that modified it’s usage in some very interesting & potentially helpful ways:

Stochastic perturbations to dynamical systems: a response theory approach. (Valerino Lucarini 2011). http://arxiv.org/ftp/arxiv/papers/1103/1103.0237.pdf

The paper assesses the impact of stochastic perturbations in the form of additive or multiplicative noise to deterministic dynamical systems using the Ruelle response theory.

I found this quite intriguing especially given most species distributions are log normal and are well suited for multiplicative approaches using the geometric mean. Thus our lab is delving into how we might apply this system to vegetative community dynamics.

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