Should journals invite submissions from preprint authors?

The Molecular Ecologist is conducting a survey on whether journals such as Molecular Ecology should directly contact authors who’ve posted preprints, inviting them to submit those preprints to the journal. Cool survey. Go fill it out, then come back here to talk about it.

This is an interesting issue that I’ve been meaning to think more about. Many journals already encourage their editors to invite submissions of preprints, and some even have editors whose job it is to identify preprints to invite for submission. So here are some thoughts off the top of my head, offered in the spirit of thinking out loud and learning from commenters who’ve thought more about this topic than I have.

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Book review: Improbable Destinies by Jonathan Losos

Jonathan Losos is one of the world’s most eminent evolutionary biologists. Last year he published his first popular science book, Improbable Destinies: Fate, Chance, and the Future of Evolution. Here’s my review. For other reviews, see The Molecular Ecologist, Science, and Goodreads users.

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What shape is the long trajectory of ecology? (updated)

It is fun to think about what shape is the trajectory of our field over the long haul, say the last century. Jeremy’s post on what topics ecologists should pursue got me thinking about this. Is the trajectory of ecology an asymptotic arc, a Michaelis-Menten or Ivlelv function. Always improving, getting  ever closer but never quite reaching the ideal? People have often suggested physics has this trajectory. Fundamental discoveries came quickly, but now more and more people spend more and more money to tease apart ever smaller order effects. Or is ecology a young field that shows a an upward straight line trend – major new advances coming in every year? Or even exponential growth once we got the groundwork laid? Or are we a random walk, wandering aimlessly around like the ants in anthill that got kicked over? Or may be we’re more systematic than those ants but we just keep going in circles? What do you think?

NB:  keep reading. If you submit your response to the Google survey it will collapse and create a large white space – keep scrolling down for the continuation.

I mentioned Jeremy’s poll got me thinking about this. One of the things that jumped out of the results to me was how often fields just got renamed. Metacommunities was rated very highly, while island biogeography was rated very low. But what is the overlap between island biogoegraphy and metacommunities? 90%? How productivity influences diversity was low, but BEF (Biodiversity Ecosytem Function) is trendy and is the exact same two variables with the direction of causality flipped. And diversity-stability was trendy – diversity stability is a question about how diversity affects the variance of an abundance time series while the unfashionable diversity-productivity is a question about how diversity affects the mean of an abundance time series – almost certainly topics that share processes (and data sets!).Clements-Gleason is about as out of fashion you can get. But it is not unrelated to the most trendy of all surveyed topics of range shifts in response to climate change. And it is strongly related to the trendy topic Jeremy didn’t survey of viewing community assembly as a set of three filters (abiotic, biotic and dispersal). In some of these cases we have almost literally just rebranded the ideas. In others we have shed a few ancillary pieces and added a few other ancillary pieces, partially remixing, but still leaving the inner cores recognizable.

I just finished editing the proofs on a paper defining macroecology (out in GEB in a few weeks). In it I point out that macroecology (1990s-2000s) was in part a backlash against the push for reductionist manipulative field experiments (1970s-1990s), and reductionist manipulative field experiments were in part a backlash against the MacArthurian push for simple models (1960s-1970s), and now macroecology is facing a push (2010s) to become less empirical and lean more on simple models! Have we moved anywhere?

This thread of thinking brought me back to one of my comprehensive written exam questions. At the University of Arizona, we got four written questions each of which was assigned a time frame of 3-5 days. These were fun questions and gave an opportunity to really think deeply about some topics (including some serious literature reading). One of my questions was in part “Briefly review the literature on interspecific plant-plant interactions”. I took a methodological approach to this question identifying the top 50 cited papers over the last 20 years in ISI Web of Science that used the phrase “plant competition”. I also reviewed several books and review papers on plant competition. Out of this I boiled out fourteen major research questions/themes in plant competition. They are listed in table 1 below. Then, just because I like to cause trouble and fervently believe in knowing the old literature, I dug out Clements’ et. al 1929 book “Plant Competition” (PC in the table) and Clements’ 1933 book on “Competition in Plant Societies” (PCS in the table). I skimmed these books for whether he addressed these same 14 themes and believed the same things as modern researchers.

Guess what! I concluded that Clements had already strongly and directly addressed (at least 50 years earlier) 12 of the 14 themes and reached the same conclusion as modern researchers on 11 of the 14 (again see table 1 below). One of the themes (non-equilbrial dynamics) was somewhat antithetical to Clements world-view (although he recognized disturbance) and another theme (diffuse competition) hadn’t really emerged. And on a third (allelopathy) Clements was active in the debate but believed it hadn’t yet been proven, where as modern researchers believe cases exist where it occurs.

So if you think I’m arguing for a circular shape to the long trajectory of ecology, you are right!  I think you could make a case that is actually a spiral. We come back to the same topic, but we do it in a better, more sophisticated way each time. Certainly in my Clements example, the methods were far more quantitative, the hypotheses more explicit, the mechanisms and language far less anthropomorphic (Clements loved to analogize to battles and warfare). So maybe a spiral? But the upward aspect of a spiral is primarily to be found in methods and language, not questions. And not answers. I think you could say the same thing about studying metacommunities instead of island biogoegraphy. So I’m not convinced the rising spiral aspect is central or the most important aspect (even if it is there).

Whether you believe there is a spiral or not, I think the circle is the central defining feature of the structure of the ecological trajectory. I only have 20 years of being an academic ecologist under my belt, and I already see circles everywhere. And when I read the literature further back in time I see them much more. You’re going to have a hard time convincing me I am wrong about circles (although of course that doesn’t mean you have to agree with me – maybe seeing circles is a bias of my mental processes – I am an intellectual lumper rather than splitter).

But I think the bigger question is whether the circular nature is a good thing, a bad thing, or a neutral thing? I can easily imagine most if not all people will say that a circle, if true, must be a bad thing. Nobody talks about the circular nature of progress in physics. It sounds insulting. But I am more sanguine. I think it is somewhere between neutral and positive. For one thing, I think the cycle time in ecology is about 25-30 years (there were two full cycles between Clements and the modern papers in my comps question). Not the least bit coincidentally the generation time of scientists is about the same. This means each time around it is a new group of scientists working on the topic. And that means the full circle of topics is covered in one scientists career. That makes it look like a rather more systematic and efficient exploration of what is ultimately a finite space, doesn’t it? And even if I don’t think the spiralling higher is a prominent feature, I do think reconceptualizing a topic every 25-30 years keeps it fresh, exciting and at the forefront of ecologists’ minds. And on a purely practical level, we do have to find new framings to get funding. The only way a circle looks bad is if we compare ourselves to physics and have physics envy. I do think a saturating function is a better description of physics. But physics is a very different science – it is not multicausal. In physics they discover the first order effect and find its formula, then they discover the second order effect and find its formula, and pretty soon the next generation is left explaining a few percent of the variability. Ecology doesn’t work that way. We have a list of the 5-20 things that matter, but we cannot rank order them. They are all equal. So we spend our time focusing for a while on competition, then moving on and focusing for a while on dispersal, and then moving on and focusing on exploitive interactions, and etc. Not better. Not worse. Just different. Circles are just fine for ecology!

I find it more useful to think about the implications of being circular than bemoaning being circular. In particular, it means ecology needs to be a field that teaches (at least to its graduate students) the history of its ideas. Its one thing to go around the circle with self-awareness. Its quite another to fool ourselves into thinking we are going in a line upwards. Physicists almost never bother with citations of old ideas (e.g. Newton’s 3 laws or Maxwell’s 4 equations). But I think ecologists always will and always should know and be able to trace the roots of their ideas at least one cycle back, and ideally 2 or 3 cycles back. It keeps us humble. And you know what, even if we have a fresh take, our ancestors were not idiots – reading their work can only improve our own.

What do you think? Do you buy my circle argument? Do you think a spiral is crucially different from a circle? If we are a circle is that good, bad, or neutral? What does a circle imply for how we do ecology?


Table 1 – The 14 major questions in plant competition in the 1980s-1990s and what Clements thought about them circa 1950

Fact Clements
Plant competition exists and is common This is no news to Clements. The fact that both of the references have the phrase “plant competition” in the title and describe numerous experiments on this subject is enough.
Plant competition is often highly asymmetric Clements regularly uses terms like dominant and subdominant. He understood the relation to size as well. “In general, the taller grasses enjoyed a decisive advantage over the shorter, but this was often counterbalanced by an earlier start or greater resistance to drouth [sic] or cold on the part of the latter. Not infrequently one species would acquire and hold the commanding position in the community and the other would perforce content itself with a subordinate role” PCS p 26. In his review of research prior to the writing of his book, he cites many authors who recognize the importance of light (PC).
Plant competition occurs both above- and below-ground Clements regularly talks about differences in root structure or shoots as a form of competition and relates this to their roles in the community (e.g. “bisects were employed to exhibit the root and shoot relations” PC p. 39). He did not have the sophisticated experiments today that allow us to say “root competition is more important in such and such condition”
Competition is density dependent and non-linear Clements certainly understood this, although the terms were not in use in his day. His experimental growth of crops at varying densities and the record of yield clearly showed the same non-linear pattern we observe today. However, he made no attempt to tie his results to any mathematical equations or models.
Competition varies over space and time Clements was well aware of this. One section in PCS is entitled “Struggle between forest and prairie” and he explores the differentiating factors. It is also clear from his writing that he was keenly aware of variations in soil, probably much more than most plant ecologists today. In a number of his field experiments he captured drought years and he talks about how this changes things (e.g. PC chapter 6) and he designed his experiments specifically to “disclose the effect of different seasons and climates on the intensity and outcome of competition” PCS p. 24
Other trophic levels affect competition Clements has a nice discussion on how grazing (either by cows or bison) affect the competition between buffalo grass and tall grass PCS pp. 28-29. He also talks abut how he designed his experiments “to evaluate the influence of animals, especially cattle and rodents, in the process [of competition]” PCS p.24. I could not find a mention of mycorrhizae in a brief review of Clements, but they were certainly known in his time (Allen and Allen 1990 cites a couple of papers published in the 1920’s)
Allelopathy occurs Clements knew about allelopathy and was part of the debate weighing in against it. He talks about “the whole problem of toxic secretions and soil toxins, and their possible role in competition. In spite of the excellent work done by Bedford and Pickering (1914) in this field, the existence, nature and role of supposed toxic substances are still subject to grave doubt (Clements, 1921) and much more extensive ecological research in various climates and soils will be necessary to a solution” PC p.35
Productivity and disturbance affect competition Clements was well aware of the role of disturbance and productivity although he did not seem to have a clear-cut idea of increasing or unimodal curves over gradients of increasing productivity or disturbance. For example he stated “Where annual mowing is the rule, Poa pratensis invades in force and assumes the role of a dominant” PC p. 37
Plants compete for resources and R* is predictive Although he was certainly aware of the role of nutrients, he tended to downplay their role compared to today: “As to the things for which plants compete, the results show that, in general, water is the most important. Light usually comes next, with minerals a close third, though the former permits a proportionally greater reduction before becoming critical.” PCS p. 35
Plants can have differentiated niches to coexist Although the niche language was not yet in vogue, it was certainly no news to Clements. “Competition is closer between species of like form than between those of dissimilar form” PC p. 11 His description of the competition between Sporobolus asper and Andropogon furcatus gives a very detailed mechanistic description of their different niches (based mostly on drought resistance vs. growth ability) PC pp.48-49.
Non-equilibrium conditions can prevent competitive exclusion Although familiar to the with the role of disturbance (see above), I believe this idea would have been foreign to Clements.
Competition can be diffuse, non-specific, and contingent If the terms were explained, I suspect Clements would agree that this was true, but I also think it was not central to his way of thinking. Most of his experiments were pairwise.
Competition can be hierarchical Clements had no doubts of this. See the quotes under the asymmetry section. Again, he did not have the neatly defined theory of inclusive niches and centrifugal organization as we describe it today, but he knew the mechanics of systems that fit this description.
Competition influences succession Clements has a five page review of the relation between succession and competition (PC p. 21-26). This may be one area in which he went further than people accept today. For example, “the outcome of each period of competition is the dominance of the best-equipped community, until the incoming of prairie or forest puts an end to the waves of invasion and conquest” PCS p. 36

Poll results: Which classic topics do ecologists care about? And which ones do they think ecologists collectively should care about? (UPDATEDx2 with more results and link to full dataset)

Recently I polled readers on which classic ecological topics they personally still care about, and which ones they think ecologists collectively should still care about. For comparison, I also asked about a few contemporary and applied topics. Respondents were asked to indicate the level of care on a 4-level scale from “don’t care/shouldn’t care” to “care a lot/should care a lot”. I coded those levels numerically as 1-4, which is fine for my crude analytical purposes.

The results were pretty interesting! (UPDATE: scroll down to the bottom for the full results table. And here’s a link to the full dataset.)

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Poll: which classic ecological topics do ecologists still care about? (UPDATE: poll now closed)

The research foci of ecology (or any scientific field) change over time. Some questions get answered, and so everyone stops working on them. New questions get asked. Some research approaches turn out to be flawed, and so everyone (hopefully!) stops using them. New techniques get adopted. Or maybe everyone just gets bored with studying or arguing about the same old stuff and decides to go do something else.

Those changes often are contested. For instance, expert ecologists often disagree on whether the leading questions of the day have been answered, or else agree that they’ve been answered but disagree on what the answers are! “Revisiting a classic longstanding question” is hard to distinguish from “beating a dead horse.” One person’s bold hypothesis is another person’s vague arm-waving. What looks like the next big thing to one ecologist can look like a trendy bandwagon to another. A result that one ecologist sees as raising important new questions can look trivial to another. Etc.

These changes also aren’t easy to measure. For instance, just because lots of papers continue to cite a classic idea doesn’t mean that idea is still a live topic of ecological research. So citation analyses only provide a crude and error-prone window into what topics ecologists care about these days.

So, my solution is just to ask y’all what classic ecological topics you still care about! 🙂 Below the fold is a fun poll. For each of a number of classic fundamental ecological topics (plus a few contemporary and applied topics, for comparison), you’re asked two questions. How much do you personally care about the topic? And how much do you think ecologists collectively should care about the topic? They’re all multiple choice questions, so the poll should be quick to complete.

A few preliminary remarks:

I’m reluctant to define “care” too precisely. A topic you care a lot about is one that you, well, care a lot about, whether or not you work on it yourself. A topic you think ecologists collectively should care a lot about is a topic you think ecologists should devote a lot of research effort towards, should probably teach to students, etc. Conversely, a topic you think ecologists shouldn’t care about is one that you think nobody should research any more, maybe shouldn’t teach to students, etc.

Note that your own personal level of care about the topic might or might not match how much you think other ecologists should care.

Please skip any topic that you’ve never heard of.

As always, this poll isn’t a rigorous random sample from any well-defined population. It’s intended as a fun conversation starter. Looking forward to your responses! 🙂

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How to revolutionize a scientific field in five not-so-easy steps

Just finished reading this very interesting 1971 address to the American Economics Association by Harry Johnson. He asks what determined the speed of the Keynesian revolution in economics, and the monetarist counter-revolution. In it, he suggests that a revolutionary theory has the following five characteristics:

  1. It has to attack–and ideally reverse–the central theoretical proposition of the prevailing orthodoxy. Ideally, the motivation for the attack should the inability of orthodox theory to explain some important empirical data.
  2. It has to be new, but yet also incorporate as much as possible of the less-disputable bits of the prevailing orthodoxy. Pulling off this apparently-contradictory trick generally requires putting old wine in new bottles: renaming established concepts without admitting that you’re doing so. It also can involves shifts in emphasis, for instance by emphasizing the importance and non-obviousness of points that were previously considered unimportant and obvious.
  3. It has to be too difficult for senior people to bother to understand, and somewhat-difficult-but-not-too-difficult for junior people to master. This gives junior people a way to work around the conservatism of senior leaders in the field, a reward for doing so, and a sense of belonging to a shared intellectual project.
  4. It has to offer some low-hanging fruit, especially to empirically-oriented researchers (as opposed to theoreticians). Ideally, it will give the junior people who master it a straightforward, “crank the handle” methodology for producing publications.
  5. It has to pick out a new, measurable empirical pattern or relationship. A stylized fact that empiricists can target for further investigation. This goes hand in hand with #4.

This story seems to fit the potted history of 20th century macroeconomics pretty well, though of course I’m no expert. So here’s my question: does it fit any revolutions in ecology? And does lack of any of the 5 attributes on this little list explain the failure of any attempted revolutions in ecology?

Just off the top of my head, I’m not sure ecology has had any revolutions that fit this scheme perfectly. Maybe that’s because, to have a revolution, there has to be an orthodoxy to revolt against? Can a scientific field in which there is no prevailing orthodoxy, or that arguably isn’t even a single discipline at all, be revolutionized?

The MacArthurian revolution starting in the late ’50s does seem like it fits some of the items on this list (see also). I’d say it fit #3-5 fairly well, and arguably #2 as well. Not so sure about #1 though.

The counter-revolution against (what was taken to be) the MacArthurian view in the late ’70s and early ’80s (the “null model wars” et al.) definitely fit #1 and I suppose arguably fit #3-4. Not sure about the others.

The attempted revolution of Hubbell’s neutral theory definitely  appeared to have #1, 2, 4, and 5. (Aside: neutral theory is a great case study for how an idea can take off in part by being widely misunderstood). Not sure about #3 though. And the revolution failed once everybody realized that it didn’t actually have #1 and #4.

What do you think? Have there been revolutions in ecology, and if so, have they fit this 5-part template? Looking forward to your comments, as always.