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.


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! 😛



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

  1. I’m not as aware of how common waxing and waning of interests is in Ecology, but I know for bio-theory people like me, often old papers and topics will re-surge multiple times, and often the most useful/interesting papers will have been written in the intervening times when most people weren’t looking. This is true in my main area (Turing instabilities) as well as with other areas I’m interested in, such as synchronisation (wherein I have definitely gained from reading your papers on the topic). I understand the perspective of a field will matter a lot for the near-term prospects, but in the history of science altogether sometimes “dead-ends” have been resurrected to be given new life, and it was quite valuable for some people to be pursuing these at the time.

    • “often the most useful/interesting papers will have been written in the intervening times when most people weren’t looking.”

      Interesting hypothesis–it’s an interesting variant on the notion that intellectual diversity is a form of insurance or “bet hedging” for scholarly fields.

      Trying to think of examples. Off the top of my head, I guess David Sloan Wilson’s (1975) trait group model of group selection might be an example of someone doing interesting work on a topic most had abandoned, thereby reviving interest in the topic?

      • Multilevel selection is what immediately came to my mind when you mentioned “Buddy Holly ideas”

  2. Another striking feature of the papers on the first list is just how many are purely descriptive. The next time someone complains that ecologists don’t value descriptive work any more, they should be pointed to that first list.

    • This is what struck me too. Despite being somebody who has contributed my fair share of perspectives and reviews, and working on global change, it kind of jumped out at more there are not many papers that could be said to “advance our understanding of how the world works” – you can extend that to no theory, but I mostly mean it in even a much more broad sense here.

      There’s a decent mix of such papers in the 3rd group. But I assume that there are a LOT more than 20 papers ranked above those to get to the 3rd group.

      • “there are not many papers that could be said to “advance our understanding of how the world works”

        Yup. One “recipe” for a potentially high-profile ecology paper is “produce a colorful map describing global change in some variable”.

        “But I assume that there are a LOT more than 20 papers ranked above those to get to the 3rd group.”

        Yes, there are hundreds of ecology papers published in the last 10 years that would show up further down one of the first two lists, but that are more cited than some or all of the papers on the third list.

      • Oh, and re: “no theory”, I definitely do not have the patience to scroll through however many pages of WoS search results you’d have to scroll through to get to the most-cited ecology theory paper published in the last 10 years (“Perspectives”, “frameworks”, and “syntheses” definitely don’t count as “theory”)

      • Hi Jeremy; thank you for the compilation, which reinforced my previous bias that stat methods and contributions to ‘understanding ‘ the biodiversity crises [ ecosystem services, etc] dominate ecologists thinking at present, as do group reports as a publication mode. Maybe, but see below.
        I have 2 small thoughts to contribute.
        first, some of the descriptive papers are not merely descriptive, but use comparative analysis to find empirical generalizations; while I have not read many of these papers, some in category 2 are of this type.This type of paper is very useful as the beginning for further analysis. And some areas,[ eg, like allometric analysis of life histories], really demands a comparative approach. Of course, the topic themes of the comparative analyses are diversity oriented in this collection.
        Second, its not quite true that conceptual, idea, theory papers are ignored at present….If one takes a broader view of scientific impact. Staying with citations, there are surely papers published before 2008 that are well cited during the 2008-18 decade. For example using the last 7 yrs citation record [ to make a fair comparison since some of the above don’t have a full 10 yrs of citations], I provide the following 3 examples. Jim Brown’s[ et all] 2004 call for a METABOLIC THEORY approach to ecology is cited about 2000 times in the last 7 years.
        Our 2001 Science paper adding temperature to body size in the determination of metabolic rates [ and other biological rates ] is cited 1000 times over the 7 yrs; and the Marginal value foraging paper of 1976 is also cited about 1000 times over the 7 yrs. So I think the more interesting question is why NEW THEORY, CONCEPT papers have recently become so less impactful?

      • @ eric:

        Yes, one important role of some descriptive/comparative papers is to establish “stylized facts” that give theory a “target to shoot at”, something to explain. I have some old posts on that which I’m sure you’ve seen, but for other readers who may have missed them:

        And yes, restricting attention to papers published in the last 10 years is a quite artificial restriction that makes my little list a poor guide to “what are the currently-influential theoretical ideas in ecology”? As you say, metabolic theory remains influential and oft-cited, even though many of the key papers were published more than 10 years ago.

    • Hi Jeremy; We apparently disagree as to the usefulness of comparative analysis for teasing out patterns. Many of the ones I know best are certainly not STYLIZED FACTS as you define them, in that they are the result of [sometimes] decades of careful research and make use of very good data. many are numeric, and not qualitative.
      BUT, you are correct that ecologists often stop with the discovered patterns, and don’t use it to look for some deeper explanation. Fisheries has several, including some across- population numeric rules that are 50 yrs old, and have remained the same in numeric value for decades [ exception: being addicted to statistics, fishery scientists periodically DEMAND that estimating this or that use THEIR new stat method; they particularly like it when the new method revises some old number].

      So why do ecologists show so little interest in probing comparative patterns for some deeper explanations? I know why for fishery scientists: they want to use the comparative rules in management models and the numeric rule itself does that quite fine, without any deeper rational.

      • Oh, I agree that comparative analysis can reveal well-established quantitative patterns, not just stylized facts. Didn’t mean to imply otherwise by linking to my old stylized fact posts.

        “So why do ecologists show so little interest in probing comparative patterns for some deeper explanations?”

        Your remark has me recalling an old comment here (can’t recall from whom–Ben Martin I think?) to the effect that most ecologists aren’t really interested in the branching circulatory system optimization model at the core of the metabolic theory of ecology. But they like the fact that that optimization model exists, because then when they’re using allometric relationships to make predictions, they feel like they’re using a mechanistic model rather than just a purely statistical pattern with no deeper rationale. Even though they of course don’t actually need that deeper rationale to make the predictions they’re making.

      • One goes deeper into ‘well believed comparative patterns’ for the same reason Newtons laws of motion are more interesting than Kepler’s laws for planetary motion; with newton’s dynamics one can recover kepler’s ‘laws’ and then SO MUCH MORE. Its the so much more that interests me.

  3. It amuses me that the most-clicked link in the post so far is to Rockstrom et al. 2009. That’s predictable of course, that people would click the first paper on the first list. But I got a chuckle out of it anyway. The paper that already has gotten the most attention over the last 10 years is getting…more attention!

  4. 1 – Titles matter. Anything that says “A safe operating space for humanity” in th title is going to get a lot of reads, and maybe citations – even if it’s wrong in its details, which it inevitably must be given the shifting goalposts of what can be considered safe.

    On that theme I just finished reading “The rise and Fall of the Dinosaurs: A new history of a lost world”. Now THAT’s a title with everything going for it: drama and tragedy (rise and fall); novelty (a new history), and mystery (lost world).

    2 – Yes. Regardless of who gets cited, we need a diversity of approaches – let a thousand schools of thought contend!

    3 – It is also probably inevitable that major review papers and syntheses will get cited a lot, as well as stats methods paper (which is a little sad).

    4. Keep calm and ecologize on!

  5. “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.”

    Great post. I don’t think it means your work is disconnected, just that number of citations doesn’t necessarily equal impact. As you say, most of these papers are cited in the first few lines of a papers when authors are trying to set their study within the global frame, even if it has nothing to do with the study (and even if the author hasn’t read it fully!). I think ‘highly-cited’ by default can only apply to generalised broad-scale work, because it will always be more applicable as a citation to a broader range of scholars (not just ecologists).

    And maybe there’s another story here…the increasing need to ‘cite something’ to back up statements, even broad general statements we all know are true like “Biodiversity is in decline globally…”

  6. Via Twitter, a suggestion for one (crude) way to separate truly influential citations from others:

  7. Navel-gazing aside: I’m surprised this post drew a *lot* of first-day traffic by our standards (well over 1000 views on the first day). And it did so despite drawing only modest interest on Twitter in terms of likes and retweets.

    I confess this bums me out a bit. Because personally, I think this is a pretty boring post. From my perspective, it’s a rerun of a post I’ve written twice before. And surely every ecologist knows which sorts of ecology papers tend to get most highly cited these days without me having to look up the data (right?). In contrast, I worked hard to promote my recent big post on gender diversity among newly-hired ecology faculty. And that’s a much more important topic than “what’s the most cited ecology paper”, the data required much more effort on my part to compile and revealed a much less-obvious headline result, and the post was much more widely retweeted. And yet it drew less traffic and fewer substantive comments than today’s post (maybe in part because I put a summary of the key points above the fold?). This is only an anecdote, obviously, so it’d be silly to read anything into it. I just always get slightly frustrated when audience interest in a post doesn’t line up with what I think the post “deserves”.

  8. Something that popped out at me is the way these lists demonstrate the importance of having a systematic publication strategy. Many of these highly cited papers are indeed very simple and descriptive, but they are the culmination of extended research programmes.

    I haven’t read all the papers on the list, but the ones I know quite well were based on theory and empirical evidence generated by the same authors over many years (e.g. Safe operating spaces, anticipating critical transitions).

    This makes me wonder whether my thinking about novelty in ecology has been wrong. Maybe the path to producing highly cited papers is to first publish a lot of incremental research, build a body of work to establish yourself as a leader in the field and only then synthesise all this work into an accessible paper that will be cited widely?

    In other words, producing highly cited papers is not about presenting a particularly novel idea in a single manuscript, but rather by producing a coherent body of work that can be tied together in a way that is easy to understand and of interest to a wide readership.

    • Very interesting remarks.

      This is an alternative explanation for why I’ll never produce a really highly cited paper. As I said in my old “shopkeeper science” post, my work tends not to be cumulative in the way you describe. I tend to have single-paper-sized ideas. There are exceptions–I’ve done several spatial synchrony papers, and several Price equation papers. But overall, mine is not a single coherent body of work.

      And so yes, that does rule out some publication strategies for me. There certainly are people with more “coherent” research programs, who intentionally hold back from publishing results until they’ve accumulated a body of work that can be pitched as a single Nature/Science paper.

      But I don’t think your description applies to all the papers on my first two lists. Because many of those papers are the products of working groups.

  9. Although I am one of those who have aided in the high citation rates of the particular papers (!), I am also a supporter of the “shopkeeper science”: because all life scientists know that “….in studies of nature one can never predict when and where fundamental processes will be uncovered. You never know when a rock you find will turn out to be a gem” ( Greider & Blackburn in Scientific American February 1996).

    If I were a shopkeeper scientist I would use the phrases above as my motto!!!!

    To further support this, I remind to you all the “Unusual Origin of the Polymerase Chain reaction” by K. Mullis, again in Scientific American some 28 years ago. A lovely story for all scientists where rocks were shown to be….gems!!

  10. Via Twitter:

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