Senior Oikos editors Dustin Marshall and Dries Bonte have a great piece on why they reject most proposed Forum articles. If you don’t know, Forum articles are opinion and perspective-type pieces, often used by Oikos authors to try to influence the direction of ecology. Turns out many proposed Forum articles share some common flaws. Below are some musings on the broader issues raised by Marshall & Bronte’s piece, including a grouchy rant about “conceptual models”.
Their paraphrased advice, with some choice quotes to encourage you to click through:
- DO slay zombie ideas. “[A] single feature unites the best [Forum papers]: the author felt compelled to write it. The most effective Forum pieces are those that the author felt just had to be written, that the field was limping along under a misguided principle, that key principles were misunderstood, or despite what the field thought it knew, it actually didn’t.”
- DON’T just tell readers that your new framework/approach will work–show that it does work, empirically. “[T]here are lots of approaches/frameworks/
model systems out there, an overwhelming number actually…[W]e see the appeal of writing a Forum piece to catalyse the uptake of some great new thing. The problem is, we rarely see such an approach succeed. At the very least, ecologists are likely to be wary of a new thing until they see the proponents of the thing successfully tackle a range of problems themselves.”
- DON’T try to use a Forum paper to respond to someone who said something about your work that you didn’t like. “We do not publish such exchanges in OIKOS as we have not seen much evidence that they are productive.”
Re: #1, I’m glad to know Dustin and Dries would’ve approved of Fox (2013), because that’s exactly how I felt when writing it.* 🙂
Re: #1 and 2, there’s something of a tension between them. There aren’t many papers that show serious problems with existing ideas (#1), and replace them with new ideas, and show empirically that those new ideas work (#2). That’s just a lot to do in one paper.
Re: #2, for better or worse (and it is some of both), Marshall & Bronte are right. Ecologists mostly won’t give up on an established approach, no matter how flawed, unless there’s a direct replacement, because basically nobody ever considers “go work on something else instead” as a “replacement”. I disagree with this attitude, but that’s the way it is, and in fairness it’s not unreasonable. Similarly, in order to adopt some new approach, ecologists usually need to be convinced, with data, that it’s an improvement on existing approaches to the same problem. And in order to adopt some new conceptual framework, research direction, etc., ecologists usually need to be convinced with data that it’s worth pursuing (and ideally, that pursuing it would be an easy route to a quick, high profile paper). There are exceptions, of course. For instance, Leibold et al. 2004 Ecol. Lett. kicked off the metacommunity bandwagon without any new data, new analyses of existing data, or even new theory. But the exceptions are rare. My own personal experience backs this up. One reason among others that Fox (2013) hasn’t had much impact is that I only talked about how not to study disturbance-diversity relationships, without showing, or even telling, how to do it (in my defense, I was up against the length limit). And my proposal for using the Price equation to study biodiversity-ecosystem function relationships (Fox 2006 Ecology) was rejected after review by Nature because I didn’t include any empirical examples. I added in several empirical examples and got good reviews at Ecology. And even then nobody else took up the approach; showing that your new approach works with real data is necessary, not sufficient, to get others to take it up. That may be changing–Winfree et al. 2015** is an empirical application of my Price equation approach that seems to have made a bit of a splash and shows signs of catalyzing wider take up of the approach. As another example, think of Peter Chesson’s work on coexistence theory, widespread interest in which is finally taking off in large part because a critical mass of people have started applying it to data.
Re: #2, specifically the “there are lots of approaches/frameworks/model systems out there” bit, I’m going to be blunter than Marshall & Bronte. “Perspectives”, “approaches” and (verbal) “conceptual frameworks” are a dime a dozen.*** Everybody with a Ph.D. already has their own perspective on the world, their own verbal conceptual framework, and their own toolkit of preferred approaches, thank you very much. So when you propose new ones, you’re not filling a need. Nobody wants to read an advertisement for your own verbal conceptual framework or preferred approach, dressed up with made up figures. This is true for anything that could be broadly classified as arm waving: verbal “frameworks”, new “perspectives”, verbal and conceptual “models”, “new research directions”, “syntheses” that comprise speculation about possible links between topics X and Y****, (pseudo) hypotheses that basically amount to “X somehow affects Y”, big “questions” that are way too vague to actually be answerable…all that stuff is cheap and easy. The progress of ecology is not limited by lack of any of that stuff. The world would be a better place if everyone stopped trying to get a paper out of the first five minutes of their job talk, the first page of their working group proposal, or that conversation they had in the bar at the last conference they attended. But don’t just take my word for it. DiRienzo and Montiglio (2015) is a fine critique of the value of verbal conceptual frameworks and related flotsam in the context of behavioral ecology. And here’s Charley Krebs calling out pseudo-hypotheses in the context of biodiversity-ecosystem function research.*****
Another thought: except in exceptional cases, influencing the direction of your field isn’t something you can do with a single paper. It ordinarily requires you to use all the tools at your disposal. A whole series of papers on your idea. Giving lots of talks on your idea. Organizing symposia on your idea. Organizing working groups on your idea. Training grad students and postdocs who go on to have success further pursuing your idea. Etc. Which is why I continue to wonder about the influence of this blog. Is blogging a good way to be influential, because the form lends itself to revisiting topics and repeating yourself? Is it a good way to be influential because you can reach a lot of people repeatedly, so that the little intellectual nudges you give your readers collectively add up to a lot of cumulative influence over time? Or is blogging a poor way to be influential, at least on its own, just because no one tool is very influential on its own? Or a poor way to be influential because blog posts are too transitory? Like how repeatedly tossing pebbles into a lake repeatedly creates ripples on the water’s surface, but doesn’t have any lasting effect on the lake once you stop tossing?****** I of course have a (tentative) answer in mind, but I’m curious to hear what others think.
Finally, re: #3, I think Brian has a draft post in the works on best practice in writing and responding to comments on published papers.
*Although ironically, I originally submitted Fox (2013) to Oikos as a Forum paper. It was rejected. But it was a totally different paper then–literally just my original zombie ideas blog post. As I recall, the editor and (especially) one of the referees weren’t comfortable with the tone and rhetoric. I respectfully disagreed at the time, but looking back I think the editor did me a favor by rejecting it. The published version is a much better paper, and I now agree that the sort of writing that works on a blog isn’t always a good fit in a paper (not that papers always need to be written in a dry style of course). A reminder, if one was needed, that rejection can really improve your papers. And that rhetoric in scientific writing is a topic on which there’s lots of scope for reasonable disagreement.
**As always, I’m using examples from my own work not for purposes of tooting my own horn, but because those are the examples most familiar to me.
***I haven’t been this blunt on the blog in a long time. I’ve intentionally dialed back on my feistiness in the last year or two, in an effort to present the best side of myself rather than the worst side. But the feisty side of me isn’t all bad, and lately I’ve been wondering if my writing has been playing it too safe. So welcome back, 2011 me! Try not to upset too many people. 🙂
****How come you never see anyone argue that topics X and Y are unlinked? Or at least, that the connections between X and Y are sufficiently weak/indirect/idiosyncratic as to not be worth studying?
*****I actually think Krebs is unfair in places in this piece. But he’s got a point.
******Well, unless you toss in enough pebbles to fill the lake basin. That snapping sound you just heard was the sound of my blogging-as-pebble-tossing analogy being stretched past the breaking point. 🙂
Hadley Wickham comments via Twitter:
Jeremy – good post, but I think you went overboard in your criticism of conceptual models. Often times, even if a model can’t be made fully quantitative at the time … and, after all these years, how many insightful models are? … important new insights can be injected into the field *provided that* those insights are supported by empirical facts. I like to think that I helped do just that, long ago, but explaining how the “costs of transpiration” (in terms of allocation to roots, or decreased photosynthetic capacity if inadequate energy were allocated to roots) provided the key to understanding leaf adaptations to variations in moisture or nutrient supply. It was one way of finally coupling photosynthesis and transpiration in an economic model for, essentially, optimal foraging theory in plants. I have another paper along these lines – involving what I call “the hole in Darwin’s atoll theory” – that I’d like to submit this year, raising questions about what exactly causes atolls and barrier reefs, physiologically and ecologically, which reef biologists seem not to have confronted themselves. Needless to say, I don’t have a data set based on a multi-million dollar series of sensors with which to test the theory directly. But without such a theory, empiricists might never jump to what ought to be measured. At least, they haven’t done so thus far.
Good point Tom. I think your response points to a difference between the sort of insightful model you have in mind–grounded in data, proposed to explain a specific empirical fact or interrelated set of facts, and quite possibly amenable to future mathematical formalization–and the sort of less-grounded, less-focused stuff I was thinking of in the post.
On the other hand, I can certainly think of some prominent cases in which purportedly empirically-grounded conceptual models in ecology have failed to lead to much empirical or conceptual progress. I’m thinking for instance of the IDH or the “hump-backed model” of diversity-productivity relationships (https://dynamicecology.wordpress.com/2015/08/03/poll-results-which-big-ideas-in-ecology-were-successful-and-which-unsuccessful/).
It’s interesting to think about why some conceptual models turn out to be a good starting point for future research, and others don’t.
Thanks, Jeremy. Three points in response that may be of general interest:
1. As someone who has long been involved in generating and testing ecological theory, I’ve come (reluctantly) to the conclusion that the most POPULAR theories (and the blog post you cite is all about popularity, IMHO) are often simplistic. That can, in fact, be their mass attraction – people with very little understanding of the complexity of natural systems can get a grip on a couple of ideas and their ramifications, and be sold by them. Examples 1 and 2 par excellence, IMHO: R* and CSR theory. R* can NOT work for a lot of resources, and there are piles of evidence against it, and yet the masses buy it. Ditto CSR theory (especially the S part, which can NOT work, and is based on a fundamental misreading of the facts).
2. To me, it is surprising that some contributions (esp books) turn out to be hugely influential even though, in detail, they are massively wrong. Examples 1 and 2, par excellence, in plant ecology and evolutionary biology: EJH Corner’s Durian Theory and GL Stebbins’ Evolution above the Species Level. Both inspired large numbers of people to begin studying tropical plant ecology and evolution, and the phylogeny and adaptive evolution of the angiosperms. Count me among them. But both of these contributions turned out to be simply wrong on most of the details. In this case, i think it was the vision and the persuasive writing style of both authors that came across … and indeed inspired lots of people to work on those visions, produce the first real data bearing on them, and in the process uncover a different and much more complex set of truths. Which, in the fullness of time, is not a bad thing.
3. Some ideas prove extremely fruitful in the long run, and we should not quickly write them off in the short term because of supposedly negative findings. Example: the Janzen-Connell effect. One could be forgiven if, in the early 80s, you viewed that theory (or at least the Janzen version) as dead due to Steve Hubbell’s initial snapshots of tree distributions in dry forest in Costa Rica and rain forest on BCI. But the data now (much of it gathered by folks being inspired by Hubbell’s initially incorrect views, and certainly his approach) show pretty overwhelming support for the JC effect. Someday, I hope that similar support will emerge for my context-dependent version (Givnish 1999) of the JC effect, positing that it should be more powerful and support higher levels of diversity in rainier and less seasonal forests, where physical conditions are less likely to limit the activities of many natural enemies of plants, which tend to be small and desiccation intolerant (e.g., insects, fungi, nematodes). Another potential example which you cite as being ± on the dustbin of history: the humpbacked model for plant diversity. I’m well aware of its shortcomings, and those of the somewhat related IDH theory, and have closely read the critiques. But Fraser et al. 2015 (Science 349:302-305 seems to resuscitate the humpbacked theory. So, pacé Huston and Grime, the humpbacked theory may yet come back into popularity!
“Some ideas prove extremely fruitful in the long run, and we should not quickly write them off in the short term because of supposedly negative findings.”
I have an old post on “Buddy Holly ideas”, good ideas that died before their time. Relevant here because the best way to recognize Buddy Holly ideas is in retrospect, after they’re “raised from the dead” by subsequent work. As I recall, we struggled to come up with examples of Buddy Holly ideas. Once an idea gets enough of a foothold in ecology, it’s rare for it to be killed off (https://dynamicecology.wordpress.com/2015/06/30/whats-the-biggest-idea-ecologists-have-ever-permanently-rejected/) Your suggestion of Janzen-Connell sounds like a rare good example of a Buddy Holly idea. As I recall, I think the only good example we came up with in the original comment thread was group selection. And even that’s kind of debatable because naive “good of the species” thinking really was killed off for good (as far as I can tell as an outsider…). The subsequent revival in the wake of George Price, D. S. Wilson, and others was a more sophisticated body of ideas centered on multilevel selection/kin selection.
Re: Fraser et al., no. Will have more on this in a future post. But for a preview, have a look at the next issue of Nature…
If nothing else, blogs are valuable because they help create novel connections within people’s minds regarding the topical materials. You may not revolutionize the field you blog about, but you do plant the seeds of ‘huh’ into people’s brains.
The work that Richard Feynman won the Nobel Prize for was inspired by watching a plate that somebody through in his university’s cafeteria. While probably not so grandiose, I wouldn’t be surprised if the rewards of blogging’s seeds are more influential than they appear on the surface.
Thanks Tor. It’s cheering to think that all the half-baked analogies I toss around might be planting some useful seeds. 🙂
And there’s more to come: Brian has a post in the queue connecting biodiversity to pizza… 🙂
“Things that make you go ‘huh'” would’ve been a good tagline for this blog. 🙂
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