The most-cited ecology papers published in the last 10 years, and why thinking about them bums me out a bit

Six years ago, I invited readers to guess the most-cited ecology paper published in the previous 10 years. Ecology’s most-cited papers are a window into where the field is at and where it’s going. An imperfect and distorted window, of course–only a few types of ecology papers, on a few topics and published by a few journals, have any chance of becoming really highly cited. But a window nonetheless. After all, the papers that become very highly cited are no accident. Rather, they reflect the research interests and citation practices of large numbers of ecologists.

Earlier this month I decided it would be fun to repeat that exercise of six years ago and look up data on the most highly-cited ecology papers published in the last 10 years–forgetting that I already had repeated it just two years ago. Crud. They say the memory is the first…wait, what was I talking about?

But if forgetfulness is one of my endearing features, another is laziness. Having spent several hours researching and writing this post, I’m loath to just junk it. And FWIW, I have some new thoughts on this little exercise and what it says about my own research program.

So below the fold are Web of Science data on three categories of papers. First, a list of the most highly-cited ecology papers published in the last 10 years (in any journal, not just ecology journals). That list is entirely comprised of papers on just four broad topics. So my second list is the most highly-cited ecology papers published in the last 10 years that aren’t about those four broad topics. That second list is entirely comprised of just four types of papers (e.g., meta-analyses). So my third list is the most highly-cited ecology papers published in the last 10 years that aren’t about any of those four broad topics and that aren’t any of those four broad paper types. Some discussion follows the lists. Please alert me to errors and omissions, and I’ll update the post as needed. Some of my searches were WoS topic searches, which tend to miss a lot of papers.

Ok, here we go! Drumroll…

(image source)

The most-cited ecology papers published in the last 10 years

1. Rockstrom et al. 2009 Nature. A safe operating space for humanity. Cited 3051 times as of mid-Oct. 2018. Yes, your mileage may vary on whether this counts as “ecology”, but it’s my list so I’m counting it.
2. Huttenhower et al. 2012 Nature. Structure, function, and diversity of the healthy human microbiome. 2979 citations.
3. Bolker et al. 2009 TREE. Generalized linear mixed models: a practical guide for ecology and evolution. 2960 citations.
4. Halpern et al. 2008 Science. A global map of human impact on marine ecosystems. 2372 citations.
5. Nakagawa and Schielzeth 2013 Methods Ecol Evol. A simple and general method for obtaining R² from generalized linear mixed-effects models. 2342 citations.
6. Diaz and Rosenberg 2008 Science. Spreading dead zones and consequences for marine ecosystems. 2278 citations.
7. Phillips and Miroslav 2008 Ecography. Modeling of species distributions with Maxent: new extensions and a comprehensive evaluation. 2152 citations.
8. Jones et al. 2008 Nature. Global trends in emerging infectious diseases. 2099 citations.
9. Hansen et al. 2013 Science. High-resolution global maps of 21st century forest cover change. 1984 citations.
10. Elith and Leathwick 2009 AREES. Species distribution models: ecological explanation and prediction across space and time. 1942 citations.

I could keep going, but honestly it’s boring. It’s just a list of (i) review and perspectives papers about global change that were published in Nature or Science, and papers on (ii) popular statistical methods, (iii) microbiomes and (iv) ecosystem services. They’re all the sort of papers everyone cites either in the first paragraph of the introduction section (even if that’s not really what the paper is about), or else in the subsection of the methods called “statistical analyses”. Hence the next list. Notice how much lower the citation counts are…

The most-cited ecology papers published in the last 10 years that aren’t about global change, statistical methods, ecosystem services, or microbiomes

1. Scheffer et al. 2009 Nature. Early-warning signals for critical transitions. 1316 citations.
2. Cavender-Bares et al. 2009 Ecology Letters. The merging of community ecology and phylogenetic biology. 927 citations.
3. Chave et al. 2009 Ecology Letters. Towards a worldwide wood economics spectrum. 921 citations.
4. Nathan et al. 2008 PNAS. A movement ecology paradigm for unifying organismal movement research. 901 citations.
5. Jetz et al. 2012 Nature. The global diversity of birds in space and time. 880 citations.
6. Vila et al. 2011 Ecology Letters. Ecological impacts of invasive alien plants: a meta-analysis of their effects on species, communities, and ecosystems. (Aside: yes, you can argue that this should count as a paper about global change.)
7. Kattge et al. 2011 Global Change Biology. TRY – a global database of plant traits. 840 citations.
8. Brooker et al. 2008 Journal of Ecology. Facilitation in plant communities: the past, the present, and the future. 840 citations.
9. Grimm et al. 2010 Ecological Modelling. The ODD protocol: a review and first update. 818 citations.
10. Cornwell et al. 2008 Ecology Letters. Plant species traits are the predominant control on litter decomposition rates within biomes worldwide. 778 citations.

You’ll notice that those are all review papers, compilations/syntheses of existing data, or opinion/perspectives/framework papers. (Note as well that most give at least a passing nod to global change, but good luck finding many recent ecology papers that don’t.) If you’re looking for other sorts of papers, you need to keep sliding way down the logarithmic citation curve, along the ways skipping over lots of papers that would show up further down the first two lists. Hence my third list:

The most-cited ecology papers published in the last 10 years that aren’t about global change, statistical methods, ecosystem services, or microbiomes, and that aren’t reviews, meta-analyses, data compilations, or opinions/perspectives/frameworks

1. Schindler et al. 2008 PNAS. Eutrophication of lakes cannot be controlled by reducing nitrogen input: results of a 37-year whole-ecosystem experiment. 629 citations. This paper, like several others on this last list, is about large-scale human impacts on the environment, so arguably could be omitted from this list on the grounds that it’s about “global change”.
2. Mulholland et al. 2008 Nature. Stream denitrification across biomes and its response to anthropogenic nitrogen loading. 610 citations.
3. Phalan et al. 2011 Science. Reconciling food production and biodiversity conservation: land sharing and land sparing compared. 565 citations.
4. Schindler et al. 2010 Nature. Population diversity and the portfolio effect in an exploited species. 549 citations.
5. Heaton et al. 2008 Global Change Biology. Meeting US biofuel goals with less land: the potential of Miscanthus. 506 citations.
6. Sims et al. 2008 Nature. Scaling laws of marine predator search behavior. 502 citations.
7. Carnaval et al. 2009 Science. Stability predicts genetic diversity in the Brazilian Atlantic forest hotspot. 497 citations.
8. Cornwell and Ackerly 2009 Ecological Monographs. Community assembly and shifts in plant trait distributions along an environmental gradient in coastal California. 491 citations.
9. Block et al. 2011 Nature. Tracking apex marine predator movements in a dynamic sea. 480 citations.
10. Kraft et al. 2008 Science. Functional traits and niche-based tree community assembly in an Amazonian forest. 474 citations.

Discussion

For purely personal reasons, compiling these lists bummed me out. It drove home to me just how disconnected my own work is from much of the mainstream of ecology, in terms of both topics and approaches. I mean, yes, I’ve worked a fair bit on biodiversity and ecosystem function, which is connected to ecosystem services. And I’ve done review papers, done papers based on data compiled from the literature, and proposed new quantitative analytical methods. But those lines of research mostly aren’t my personal favorites, and they aren’t my strengths. My self-image, and my comparative advantage as an ecologist, is shopkeeper science. I like to think of myself as someone who has his own ideas that are of broad fundamental interest, and who pursues those ideas with models he developed himself and experimental data collected in his own lab. That’s also what many of my closest friends in ecology do, and what many of the papers I most admire do. But the potential impact of that sort of work is severely limited these days.

“Potential” is a key word in that last sentence. It’s not just that the sorts of papers I most like to write will never be very highly cited. After all, most papers on global change or statistical methods or whatever will never be very highly cited either. It’s that the sorts of papers I most like to write don’t even have the potential to be very highly cited. The reason (some) papers about global change, statistical methods, etc. have the potential to be highly cited is because they concern topics that matter to many ecologists (and to many non-ecologists, in the case of global change papers). Science is a communal enterprise. It has to be, if adjectives like “interesting” or “important” are to have any meaning when applied to scientific work. That doesn’t mean that the scientific community always correctly decides which lines of research are most worth pursuing. Bandwagons, zombie ideas, Sleeping Beauties, and Buddy Holly ideas are real. But scientists’ collective professional judgment often is reasonably good. I mean, would anyone argue that global change isn’t super-important for ecologists to study? That microbiomes aren’t one of the most important new frontiers for ecological research? That advances in computer hardware and software shouldn’t change our statistical practices? Further, ecologists’ collective professional judgment isn’t arbitrary or purely subjective, even if it’s not completely objective either. So if I choose not to work on the problems that ecologists collectively care most about, and if I can’t convince others to work on the problems I care most about, well, there’s a prima facie case to be made that I’m some combination of idiosyncratic, a poor salesman, and lacking in skills. And half-joking about how my papers are like fine wine doesn’t really address that case. I don’t actually buy that case–if I did I’d quit doing science–but it’s not obviously a completely incorrect case.*

I emphasize that I’m not criticizing work on global change, statistical methods, meta-analyses, etc. I am emphatically not one of those misguided people who thinks that anybody who does ecology differently than me is Doing It Wrong. And I don’t think my own work is unfairly neglected. I’m just musing, a bit ruefully, on the inevitability of trade-offs. If you want to do shopkeeper science–as I still do–well, the trade-off is that your “shop” will never grow into the scientific equivalent of WalMart. Which is a bit of a bummer sometimes.

*I don’t buy it in part because I think there’s insurance value for a scholarly field in having a diversity of questions and approaches. If everybody agrees on what questions to ask and how to answer them, and everybody turns out to be wrong, the entire field is at serious risk of getting stuck.** I also don’t buy it because citations are only one measure of impact. For instance, the latest Nature or Science paper on global change might well end up highly cited–because it quantifies something we already knew and cared about. There’s an important place for that. But there’s also an important place for work that discovers things we didn’t already know or suspect.

**So if ecologists ever wake up one morning and decide that their collective focus on global change was a big waste of time, well, good thing there are still ecologists like me around! 😛