What are the most influential opinion/perspective papers in ecological history?

Manu Saunders just posted, asking what makes for a good opinion/perspective paper in ecology. Manu notes the apparent lack of agreement among editors and reviewers as to what makes for a good opinion/perspectives paper. This is a topic we’ve discussed before.

One way to answer the question “What makes instances of X good?” is to look at instances of X that everyone agrees are good, and reverse-engineer the reasons why those instances are good. Or, you could identify bad instances of X, reverse-engineer what makes them bad, then avoid doing that.

For instance, last year Dey et al. (great paper) reviewed one particular kind of opinion/perspectives paper in ecology: “research prioritization” papers. That is, papers with titles like “100 key questions for the next century of ecological research” or “Emerging issues in global change research” (I made those titles up, but I’m sure you recognize the type). Dey et al. couldn’t find any detectable effect of such papers on the direction of ecological research.* So insofar as the goal of those papers is to influence future ecological research (and if that’s not the goal, what is the goal?), those papers apparently are ineffective. So perhaps “research prioritization” papers provide an example of what not to do when it comes to writing opinion/perspectives papers in ecology.

But what about positive examples? What are the most important or influential opinion/perspectives papers in the history of ecology?

In evolutionary biology, Gould and Lewontin’s “Spandrels” paper is the obvious answer. That paper was certainly influential outside evolutionary biology. And it was much discussed and much taught within evolutionary biology, though I’m not sure how many minds it changed (as opposed to merely annoying people).

In ecology, the candidates that come to my mind mostly aren’t really opinion/perspectives pieces. Leibold et al. (2004)–the paper that got community ecologists excited about “metacommunities”–is really a review of the theoretical literature. It develops a novel framework to organize the literature, and it’s that framework that made the paper so influential. I guess you could call that framework the “opinion” or “perspective” of the authors. But I dunno, Leibold et al. (2004) just doesn’t feel like an opinion/perspectives paper to me. Same thing for the enormously influential Bolnick et al. (2003; “The ecology of individuals: incidence and implications of individual specialization”). It’s a synthetic review paper, not an opinion/perspectives paper. Same for the other influential review papers discussed in this old post and comment thread.

If you count the philosophy of science papers in the famous** Nov. 1983 issue of American Naturalist as opinion/perspectives papers (and I think you should), then they’re my nominees for most influential opinion/perspectives papers in ecological history.

Levins (1992) is the only other very influential opinion/perspectives paper in ecology I can think of right now.

No, Fox (2013) is not among the most influential opinion/perspectives papers in the history of ecology, come on. Or if it is, that is a pretty sad commentary on opinion/perspectives papers in ecology!

So you tell me: what are the most important, influential opinion/perspectives papers in the history of ecology?

*Presumably because those papers tend to endorse ecologists’ existing research priorities. According to Dey et al., the #1 most common research priority area suggested by recent research prioritization papers in ecology is “climate change”, followed by “ecosystem services”. Which have been probably the two hottest areas of ecological research since the mid-1990s. At the more granular level of specific priorities rather than priority areas, recent research prioritization papers in ecology have identified a total of 2,031 research priorities. Which should surely be enough to cover everything every ecologist in the world is already studying. A perfectly fair summary of the recommendations of research prioritization papers in ecology is “Everybody keep doing what you’re doing!”

**For “famous” read “famous to ecologists who are at least as old as me,” right? It’s the opinion/perspectives paper equivalent of, like, Safety Dance, or WarGames, right?***

***Feel free to start a “paper X is like song Y” thread in the comments. 🙂 Now if you’ll excuse me, I have to go identify the ecology paper equivalent of Rock Lobster.

34 thoughts on “What are the most influential opinion/perspective papers in ecological history?

  1. I wonder if there are any impacts of “research prioritization” papers on funding programs or science policy decisions? They are the kind of evidence policy makers like and can use to push for particular funding programs, though that would be a longer impact to track given the rate at which such funding programs and government decisions tend to be made. Perhaps such papers are not really meant for other scientists …

  2. Another thought about Dey et al.: the cases I know of in which scientists effectively set research priorities are fields in which there’s a lot of central coordination of research effort around big ticket instruments. For instance, astronomers all get together and decide that the Hubble Space Telescope is their #1 priority, and say so to NASA.

    This kind of example reinforces Dey et al.’s points, I think. If the authors of research prioritization papers in ecology were actually serious about shaping research priorities in the field, they’d be conducting field-wide exercises to get all ecologists to agree on a very short list of very specific priorities, and then going to funding agencies and saying “We all agreed–only fund this short list of priorities.”

    Obviously, there’s no way that would ever fly in ecology–we ecologists don’t want to all be centrally coordinated in that way. So I don’t think there’s much point to research prioritization papers in ecology. (And I say that as someone who’s a co-author on one!)

  3. My guess is that these papers are extremely difficult to find in the ecological literature because the only ones with such a power (Levin’s 1992) are directly taken from the Physics world of ideas and heavily grounded on simple, Occam’s razor sort-of conceptualizations. Most of the ecological literature picking up on these ideas from the Physics world come in the shape of standard research papers, such as Leibold (2004), not, as you mention, as opinion/perspectives papers. And the research prioritization papers usually involve many coauthors that logically present their own interests as priorities, so they don’t really look beyond their own discipline to define what is relevant to ALL ecology disciplines. They are pretty much statistical compilations of what ecologists’ interests are and not a honest appraisal of what leads the way to ALL disciplines within ecology.

    I could think of other opinion/perspectives papers back in the big era of mathematical biology as a driving force of ecology and evolutionary biology (indeed, the spandrels’ paper is a jewel, again, from the 70’s!). In the current big-data atmosphere I can not see a way to find such an outstanding opinion piece. Excuse my negativity in this respect.

    • “Excuse my negativity in this respect.”
      Oh, I agree with your negativity when it comes to research prioritization papers! Someone else will have to excuse both of us. 🙂

    • “And the research prioritization papers usually involve many coauthors that logically present their own interests as priorities, so they don’t really look beyond their own discipline to define what is relevant to ALL ecology disciplines. They are pretty much statistical compilations of what ecologists’ interests are and not a honest appraisal of what leads the way to ALL disciplines within ecology.”

      There’s an analogy here to many universities’ “strategic plans”. Those plans supposedly set the university’s research and faculty hiring priorities. But in practice, they’re usually so broad and vague that they encompass everything the university is already doing, without prioritizing anything over anything else. Which is understandable, because if your “priority areas” don’t cover all of your faculty, you’re going to seriously upset whichever faculty don’t feel included.

  4. Should we read anything into the fact that all the good suggestions so far are pretty old? The most recent is Leibold et al. 2004, which is 17 years old. I mean, obviously you can’t tell yet if a paper published last year is going to be influential. But surely you don’t need a minimum of 17 years to tell! Were there any influential opinion/perspective papers in ecology published from, say, 2005-2016?

    • Vellend 2010 has definitely been influential, to the younger ecologists at the very least. That falls into the perspectives category right?

      • Yes, Vellend 2010 has been very influential among younger ecologists. But that’s one of those papers that doesn’t really feel to me like an opinion/perspective piece. It’s like Leibold et al. 2004 in that way. But YMMV; I wouldn’t argue with anyone who considered it an opinion/perspective piece.

      • I think “perspective” is a reasonable description. A different lens through which to view the theories and ideas that exist already. But different descriptors might fit as well.

  5. I would mention Lenore Fahrig’s papers on the habitat amount hypothesis (2013) and the effects of fragmentation per se (2017) as highly influential; I think they’re both something between a review paper and an opinion paper.

    • Yes, I thought of Lenore’s work when I was writing the post. Outstanding and influential papers. I think of them as review papers, but yes, I can see where some might consider them opinion papers.

    • Certainly very influential! But is it really an opinion/perspective piece? I’ve never thought of it that way myself, but perhaps I should?

      If that sort of paper counts as an opinion/perspective piece, then Connell 1978 (intermediate disturbance hypothesis) probably does too. So do several other influential hypothesis-development papers from the 1960s and 1970s. The Janzen-Connell hypothesis. Grime’s CSR theory. Menge & Sutherland. Etc.

  6. I certainly agree with Manu’s view that modern reviewers have lost the taste for perspective pieces and pretty much reject anything that doesn’t evolve into a full blown research paper.

    I’ve got push back on the Dey at al conclusion. Sure the “100 questions” papers are hard to be too influential because they barely contain a point to remember (rather 100 points). But 2-3 papers came out around the same time that really advocate for more attention to functional traits and they did “change” the research direction (for better or worse depending on your perspective I suppose). I put change in quotes because there was also distinctly an element of timing – catching the wave rather than creating it. But I think you have to give those papers some credit for crystalizing the moment and advancing it.

    I think there is a problem with the question though. The lines on opinion pieces and review papers are pretty blurry. Good opinion pieces are rooted in prior literature and ideas and can look a lot like review papers. And really good review papers don’t just regurgitate what 78 previous papers say but shape them into a wholly new perspective on the field (e.g. Vellend 2010).

    Similarly many papers are really putting forward a theory. But are they opinion papers if they don’t have equations and models. Several of Janzen’s speculative papers like “Why mountain passes are higher in the tropics” or “Why fruit rots, seeds mold and meat spoils” or even “Herbivores and the number of trees species in tropical forests” (the Janzen half of the Janzen-Connell hypothesis, albeit this paper does have graphs so maybe its theory and not opinion?).

    I would suggest Bob Ricklefs is another good candidate for multiple pure opinion pieces that influenced the field (beyond 1987).

    And then as you point out Jeremy are philosophy of science papers opinion papers? I would say yes. And there are several influential papers debating how to define a community. Are those opinion pieces or philsophy of science or methods pieces?

    And where do John Lawton’s View from the Park papers (which I know were key to both you, Jeremy, and I in getting into blogging). Just musings? or Opinion papers?

    My advice to editors when dealing with these types of papers is not to get too hung up on what type of paper it is – just whether it is a good paper or not.

    • And what about Homage to Santa Rosalia as perspective and influencing direction of the field paper? Or Jim Brown’s Two Decades of Homage to Santa Rosalia? Basically question posing papers like Janzen.

      Or Hutchinson’s niche as n-dimensional hypervolume (again attempted definitional papers like the papers on defining communities)?

      • Yes, if we’re counting Janzen-Connell, HSS, et al. as opinion/perspective papers, then Homage to Santa Rosalia and Hutchinson’s niche-as-n-dimensional hypervolume paper definitely count as influential opinion/perspective papers.

    • “I’ve got push back on the Dey at al conclusion. Sure the “100 questions” papers are hard to be too influential because they barely contain a point to remember (rather 100 points).”

      Interesting. Suggests that the problem isn’t with “research prioritization” papers per se, but only with those that suggest more than (say) 2-3 priorities.

      “The lines on opinion pieces and review papers are pretty blurry. ”

      I think that’s one inarguable take home message of this thread! 🙂

      “And where do John Lawton’s View from the Park papers (which I know were key to both you, Jeremy, and I in getting into blogging). Just musings? or Opinion papers?”

      They’re definitely opinion papers. A mused opinion is still an opinion. 🙂

      “My advice to editors when dealing with these types of papers is not to get too hung up on what type of paper it is – just whether it is a good paper or not.”

      That strikes me as good advice, though it does still leave open how to evaluate how good a paper is.

    • “I certainly agree with Manu’s view that modern reviewers have lost the taste for perspective pieces and pretty much reject anything that doesn’t evolve into a full blown research paper.”

      TREE would be the exception to that generalization, though? Right?

      • Agreed. Somehow people know what to expect from a journal that is 100% review and opinion. But for mixed journals that mostly publish research (whether it be Oikos or GEB) reviewers seem to just bring their “research” cookie cutter. Ecology Letters maybe has also gotten enough of an image with perspectives to get reviewers to bend too, but in my experience it is getting harder there too.

      • It’s only an anecdote, but related to the question of reviewer’s and editor’s tastes. My 2010 perspective/synthesis was rejected without review three times (in proposal form by Annual Review of EES; full manuscript by American Naturalist and Ecology Letters)

      • Interesting. Papers that are rejected without review rarely go on to become influential if/when they’re eventually published. I would be very interested to know if there’s something distinctive about the rare papers that are rejected without review and later go on to become widely cited or otherwise influential.

      • It would be interesting to know the review history of ecology/evolution papers that go on to be widely cited/influential. Put against a background of review history of random non-influential papers.

      • I didn’t know that Paine and Fox paper – interesting. A quick scan of the results suggests that in absolute numbers there are still a lot of papers that get rejected in one place and then become widely cited/influential once published elsewhere. The relationships have lots of variance. Even if the proportion is small, we’re still talking about many instances. Also – being just plain lazy here, sorry – do they correct for or deal with the fact that papers can get more citations *because* they are published in a higher impact journal? That is, if higher ranking journal X would have accepted paper Y, it likely would have received more citations than it ended up having in journal Z. I don’t know about evidence for that, but it seems *highly* likely.

      • “do they correct for or deal with the fact that papers can get more citations *because* they are published in a higher impact journal?”

        Yes, they do correct for that. See section 4.1.2 of the paper.

    • “I certainly agree with Manu’s view that modern reviewers have lost the taste for perspective pieces and pretty much reject anything that doesn’t evolve into a full blown research paper.”

      Stephen Heard apparently disagrees, suggesting that opinion/perspective papers actually are proliferating. Hard to see how they could be proliferating if reviewers don’t like them? Well, unless they’re proliferating in the form of full-blown review papers?

  7. Agree with Brian’s comment, there are blurry lines between reviews and opinoins, perhaps more so traditionally when narrative reviews were the norm (now they are not considered as rigorous as systematic/formal reviews). But as I say in my blog, regardless of the nuance of definition, the whole point of a rigorous opinion/perspective is that it is evidence based, i.e. grounded in knowledge and comprehension of existing literature. So while it may not bre presented as a formal review paper, a good opinion piece should include some sort of review and interpretation of existing literature.

    Two that are up there in the list of papers I cite/lean on quite often:
    McGill et al.’s Rebuilding community ecology from functional traits https://www.sciencedirect.com/science/article/abs/pii/S0169534706000334
    Kremen’s knowing the ecology of ecosystem services https://onlinelibrary.wiley.com/doi/abs/10.1111/j.1461-0248.2005.00751.x

    This paper from Teja Tscharntke et al was also one of the key perspectives that kicked off the ever-growing body of literature on community ecology & ecosystem function in agricultural landscapes
    https://onlinelibrary.wiley.com/doi/full/10.1111/j.1461-0248.2005.00782.x

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