The road not taken – for me, and for ecology

Everyone knows Robert Frost’s poem The Road Not Taken:

Two roads diverged in a yellow wood,
And sorry I could not travel both
And be one traveler, long I stood
And looked down one as far as I could
To where it bent in the undergrowth;

Then took the other, as just as fair,
And having perhaps the better claim
Because it was grassy and wanted wear,
Though as for that the passing there
Had worn them really about the same,

And both that morning equally lay
In leaves no step had trodden black.
Oh, I marked the first for another day!
Yet knowing how way leads on to way
I doubted if I should ever come back.

I shall be telling this with a sigh
Somewhere ages and ages hence:
Two roads diverged in a wood, and I,
I took the one less traveled by,
And that has made all the difference.

I thought of this poem a couple of times when reading this week’s issue of Nature.

The first time was for personal reasons, while reading a very nice profile of Bob Paine. The profile emphasizes that he’s been influential not just through his own work, but indirectly via all the very successful and influential ecologists who trace their “academic ancestry” back to him. This sort of thing is fun, if always a little arbitrary (most ecologists have more than one mentor during their careers, and so can be said to be “descended” from more than one person). Reading this reminded me that when I was first looking for graduate advisers, I really wanted to join the Paine “family tree”, either by joining his lab or the lab of his former student Bruce Menge. For various reasons, I went in a different direction in the end. But I’ve occasionally wondered what the road not taken would’ve been like. In some ways I might have ended up rather the same. Bob Paine, Bruce Menge, and Peter Morin (with whom I actually ended up doing my PhD) are all big believers in manipulative experiments for instance, so I’d probably still have ended up as an experimentalist myself. And they all encourage their students to develop their own projects, so I’m sure I’d have learned to think for myself no matter where I went. They’re alike in little ways too. For instance, like Bob, Peter never puts his name on student papers unless he really has made a sufficiently substantial contribution to have earned co-authorship. But on the other hand, they work in different systems and their interests and approaches differ in other ways too. I’d surely be doing different experiments and thinking for myself about different stuff had I joined the Paine or Menge labs. And while my own interests and approach have diverged from Peter’s in some ways over the years, presumably I’d have diverged from my supervisor in some different fashion had my supervisor been Bob Paine or Bruce Menge instead. Anyone else ever wonder about this? Wonder what would’ve happened if you’d chosen some other supervisor?

I also thought of the Frost poem because of the juxtaposition of the Paine profile with a piece by Drew Purves and colleagues. Brian isn’t the only one calling for ecologists to do more predictive modeling, and to take their cues from the data- and computationlly-intensive successes of fields like meteorology. In their piece, Purves et al. call for ecologists to develop “general ecosystem models” (GEMs; awesome acronym!). GEMs would be analogous to climate scientists’ general circulation models (GCMs). Purves et al. recognize that such models will be very challenging to develop, but argue that it’s feasible if we take the right modeling approach and get serious about collecting the right data. For instance, they suggest that GEMs, like GCMs, will need to be explicitly mechanistic and process-based, as opposed to purely statistical or phenomenological. They also suggest that, like GCMs, GEMs will need to aggregate or otherwise simplify a lot of underlying detail, such as lumping species into coarse trophic groups like “herbivores” and “carnivores”, and using body size allometries to estimate unmeasured parameter values. Purves et al. are speaking from experience–they’ve built a prototype GEM that produces promising results. And they rightly emphasize that if ecologists were to get serious about building GEMs, much of our data collection effort (both observational and experimental) would have to be redirected, towards obtaining whatever data are needed to reduce the most important uncertainties in the GEMs. So there’d still be place-based field research–but it would be whatever place-based field research was needed to support GEM development. I found the piece a very good and thought-provoking read from some ecologists who clearly are not hypocrites when it comes to forecasting the effects of climate change.

As I said, I found the juxtaposition of the profile of Paine with the Purves et al. piece striking, and it made me think of Frost’s poem. To the extent that ecologists ought to redirect their efforts to building, or supporting the building of, the sort of predictive models Purves et al. call for, they’ll need to direct their effort away from the sort of experiments that made Bob Paine and many of his students so influential. And indeed, the profile of Paine touches on this near the end, noting that some of his “descendants” have moved into the sort of science Purves et al. call for. Bruce Menge for instance has moved away from the sort of field experiments individual investigators can run and into large-scale, standardized data collection by big, coordinated teams. It’s the sort of data that one needs to parameterize GEMs–but also the sort of science that leaves little room for individual investigators to think and work independently. It’s very centrally-coordinated science. And while it’s science that undoubtedly raises some interesting fundamental, conceptual questions, it’s very policy-driven science. As his own “descendants” like Jane Lubchenco note, Bob Paine doesn’t have much use for “relevant” or centrally-coordinated research.

I don’t want to exaggerate here. I highly doubt that we’ll ever see a world in which literally every ecologist does the sort of work that Purves et al. call for and no one any longer does the sort of curiosity-driven, fundamental work that made Bob Paine famous, or vice-versa. But there clearly is a trade-off here, two roads diverging in a wood. And while some ecologists will always go down each road, the field as a whole–perhaps as indexed by the road more ecologists take–does seem like it may face a choice in the not-too-distant future.

20 thoughts on “The road not taken – for me, and for ecology

  1. I liked this post very much Jeremy! Very thoughtful. I too thought it highly interesting that the two pieces (about Paine and about GEMs) were in the same issue. I’ve been struggling myself with the decision which road to take, and I guess I have yet not decided. What will I become when I grow up? The eternal question…

  2. Hi!

    Nice post, I always liked Frost’s poem ever since I took English as my first foreign language, and not French. I took the more travelled road, then.

    Your mentioning of Drew Purves’s work reminds me of a discussion I had after the talk he gave at the BES Annual Meeting last December.
    I was very much arguing for another co-ordinated large-scale programme in Ecology in order to acquire relevant data in standardised ways, identify general principles (and their relative importance), synthesise knowledge and understanding that is not necessarily available in the standard literature etc., similar to the International Biology Programme 1964 – 1974 (
    I met quite a bit of resistance and my friends and colleagues were wary and dismissive of what they called a wasteful and even dogmatic top-down approach to science. Apparently the IBP is largely considered a failure. I guess they are right in a way and I don’t want to discredit or dry out funding for the curiosity-driven, maybe more idiosyncratic grass root science I myself do. But it hardly ever addresses the pressing needs of on-the-ground managers or policy-makers (see Peter Adler’s guest post where he mentions the unsexy data he thinks are needed to predict future species distributions or Robert Cabin’s book “Intelligent Tinkering”). So, my feeling is there is right now an unfortunate (?) bias towards the latter approach and we basic ecologist usually take the well-travelled road. Maybe we should be more like Frost and take the other path more often. One reason for this bias seems to be a somewhat contemptuous attitude towards abiotic factors. Population and community/food web ecologists love and hence predominantly focus on biotic interactions. This is for example reflected in that a legion of abiotic factors go, when modelled, into only a handful of parameters such as maximum intrinsic growth rate r or carrying capacity K. For the sort of models developed by Drew Purves I would assume much more data are needed on temperature optima, water requirements, nutrient concentrations etc. and how they affect and interact with the biotic interactions.


    • The IBP is indeed largely considered a failure, at least by folks I know. That’s one reason why many folks are skeptical of NEON.

      Whether this division (which I tend to think of as basically between ecosystem ecologists vs. population/community ecologists) also maps onto an interest in abiotic vs. biotic factors, I’m not sure. You could be right about that.

      • As a social insect person with a keen interest in seeing some of the output of the special focus of the IBP (Brian 1974) on social insects continued, I have a slightly different view. I think the IBP was a good starting point but never lived up because there was not enough subsequent effort put into pursuing fundamental natural history studies required to make all of the connections between populations and communities to ecosystem services. As an example, Kaspari has done some of this work (e.g. linking social insect biotic patterns to abiotic factors), but much more needs to be done on the natural history side to make meaningful connections at the ecosystem scale. I would favor top-down approaches like NEON or IBP a bit more if there were more focus on natural history as part of their mission. As a specific example, woody material decomposition is a very important ecosystem process that termites are the key players in, yet the ecology of perhaps the most important species involved in this process (the termite Reticulitermes flavipes) on the entire east coast of the US, is poorly understood, outside of its pesty habits in urban areas. Maybe its just not very “sexy” to spend one’s time working out the vagaries of termite ecology, as opposed to, say, modeling carbon flux.

      • Interesting suggestion Josh. Although this may highlight something of a contrast between the IBP and the sort of GEM-driven work Purves et al. are calling for (I’m not sure, I don’t know enough about the IBP). For GEM-driven work, whether or not we need to know about the natural history of species X will depend on whether the forecasting errors the model makes can be attributed to lack of natural history knowledge of species X. In some cases, I suppose we may need some of those details, depending on what exactly our GEM is trying to forecast. But in other cases (probably most cases), we won’t. GCMs work, and work pretty well, despite running roughshod over absolutely massive amounts of all sorts of biological and physical details. I’m sure GEMs that work will omit lots of natural history as well, or else summarize it implicitly in higher-level parameters.

      • I’m not totally sure about what exactly the concrete goals of the IBP were and why they were not achieved. It may be that ecological theory was not advanced and mainstream enough at that time to have a well-formulated framework facilitating synthesis and general understanding. More recent programmes like SizeMic ( and LEREC (–lake-ecosystem-response-to-environmental-change-/) were I think more successful because of their strong theoretical foundation and focus. Whether NEON has this background and will go beyond large-scale monitoring/data gathering I don’t know.
        I don’t think there is a division between ecologists focusing more on abiotic or more on biotic factors. I think the former are generally rather neglected. Ecosystem ecologists study things like carbon fluxes, nutrient cycling and hydrology regimes and how they affect production and fluxes of biomass etc. but not really how variation in temperature or water availability mechanistically explains community dynamics. Maybe you find this in macroecology but from Peter Adler’s post it seems not to be overly common. However, try to tell in advance and in considerable detail the seasonal dynamics of a zooplankton food web. How important is e.g. weather and how much trophic interactions? If you ask an aquatic ecologist the answer is predictable*. The few successful examples I know in predictive community ecology work well in simple and rather stable systems (Ed McCauley’s laboratory Daphnia populations, Lennart Persson’s fish communities in a sub-arctic lake, Bill Murdoch’s Californian Red Scale – Aphytis interactions on single trees) but would they work in more environmentally variable settings? Actually, taken Josh’s comment into account, they work well because there is a lot of natural history known of these model organisms when it comes to how density dependence works, what the feeding rates are etc.

        *OK, I am exaggerating. There is work on for example temperature-dependent piscivory rates or on how water transparency influences predator-prey interactions. But it seems comparatively rare and somewhat system specific.

      • Well, we do have some successful predictive population modeling in systems subject to weather variation, including some of the examples you rightly cite. But yes, in most of those examples it turns out to be most important to get the density dependence right. Now, whether those systems are “simple” is whole ‘nother question! (perhaps “low dimensional” might be a better word?)

        You’re certainly right to point out that some large-scale, centrally-coordinated data collection efforts are question- or theory-driven, and others aren’t. This is a key contrast, I think. NutNet, which I’ve highlighted before on this blog, is a large-scale, centrally-coordinated but very hypothesis-driven effort. NutNet is also experimental–it involves repeating the same small-ish experiment in many locations around the world. Might be interesting to try to place different styles of ecological research in a low-dimensional space defined by a few key axes (individual investigators vs. large coordinated teams; observational vs. experimental; question-driven vs. question-free, new data collection vs. compilation and analysis of existing data; etc.) I’d be curious to see if the entire space was “filled” or if there are certain regions of the space that have never been tried (perhaps for good reason?), and how ecology as a whole has moved through the space over time.

  3. Nice post! I am a bit torn between these two paths. I think the path one prefers is largely determined by whether one sees ecology as simply being too complex to ever (or at least within the foreseeable future) understand/predict, or whether useful predictions are not so far off if we devote enough time and money to model development and data collection.
    I am not sure which group I fall into. Therefore I would suggest hedging our bets a bit. For example, by not letting data collection be so adapted to the development of any one specific model that it has little use for other purposes.
    Even if GEMs fail to ever produce useful predictions, the process of developing a model designed to “guide the decisions of conservationists and policy-makers” may prove worthwhile, for example, in identifying areas critical for model predictions that have so far be neglected.

  4. Upon further reflection, I don’t know that the field of ecology as a whole faces an irrevocable choice the way a single individual does when faced with a “fork in the road” such as a choice of graduate supervisors. Ecology as a whole has always swung back and forth between dominance by different research approaches. A big push towards the sort of work that Purves et al. call for wouldn’t necessarily lead to permanent changes in ecological research, any more than, say, the IBP permanently changed all of ecology into IBP-style science. Probably at some point we’d all start to keenly feel the limitations and shortcomings of GEM-driven science, while also feeling that further pursuit of GEMs was yielding diminishing returns, and there’d be a push to swing back towards Paine-style work, or towards some other style of work.

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