Note from Jeremy: this is a guest post from Mark Vellend
During my very first research experience in ecology (mid-1990s), Graham Bell, a famous evolutionary biologist, talked about the forest plants we were studying as if they were essentially just large and slow versions of the algae multiplying rapidly in the highly simplified test tubes of his lab. The other undergraduate field assistants and I (the “Carex crew”) – all of us thrilled to have paid jobs to tromp about in Wild Nature – felt that this perspective sucked all the beauty and wonder out of the forest that we so loved. But it stuck with me.
This is a second guest post expanding upon thoughts and some personal reflections that arose while I wrote a book on community ecology during sabbatical last year. The first post is here, and I couldn’t help noticing that it was given the tag of “New Ideas” by Jeremy. Hmmm…I wonder how we decide whether an idea is “new”? I think the answer has rather important implications for how we judge papers and the scientists that write them. All the top journals want “novelty”, but what is that exactly? And where do ideas come from in the first place?
The core idea underpinning my book is that we can organize the innumerable concepts, theories, and models in community ecology by understanding them as representing different combinations of just four high-level processes: selection, drift, dispersal and speciation. In other words, change in the genetic composition of a population is conceptually the same as change in the species composition of a community, so ecologists can borrow heavily from widely-admired evolutionary theory.
Is that a novel idea? Some say no, and justifiably so. One of the points in Janis Antonovics’ “Ecological geneticist’s creed” states that “The forces maintaining species diversity and genetic diversity are similar”, and similar arguments have been developed to varying degrees by Bob Holt (chapter in this book), Joan Roughgarden, Priyanga Amarasekare, Steve Hubbell, and others. During the time I was a student, Graham Bell and his students conducted a great many experiments on the evolution of various kinds of algae, and, as mentioned above, different forest plant species were then treated as no more than conceptual analogues of algal genotypes. So, no, the idea is not novel.
Or maybe it is. Noting conceptual parallels between two disciplines is one thing, and developing that nugget of an idea into a conceptual framework that greatly simplifies our understanding of an otherwise unruly mountain of models and theories in community ecology is quite another. Is that “novel”? Some seem to think so, while others clearly do not – most notably (and disappointingly for me) the editors of American Naturalist and Ecology Letters, who chose not to send the original paper out for review. Oh well (yes, poor me, we all get rejected I know…but it still feels crappy!).
So, for this one case study, we can provide provisional answers to our two questions. First, novelty is, to a considerable degree at least, in the eye of the beholder. It might be easy enough to identify when someone has clearly but unwittingly re-invented the wheel (i.e., a novelty claim is bogus), but once in a gray zone, reviewer 1 will say “amazing!”, reviewer 2 will say “not a chance”, and the editor (not uncommonly me) will make a judgement call, feeling rather uncomfortable and angsty doing so, but realizing that not all papers can be accepted, someone has to make the call, and it may as well be her/him. Second, ideas come from pondering, re-shaping, and developing those generated by our scientific ancestors. Stepping back from this case study, are there general categories of novelty and the origin of ideas?
I can think of a few possibilities (please chime in with others):
(1) An idea is put forward that is virtually without precedent. I’m not an expert on the history of science, but the popular story of Einstein sitting at a boring desk job, figuring out on his own how the universe works in mysterious ways we could barely imagine, seems like a type specimen for this. Here, the origin of the idea is the brain of a genius, and it represents perhaps the only “true” kind of novelty. Are there any ecological examples of this? (I don’t think Darwin counts.)
(2) An idea with clear precedence and scientific roots counters era-specific conventional wisdom. Island biogeography theory seems like a good example. It seems to be widely and justifiably (in my opinion) admired as a “big idea”, even though someone named Eugene Monroe put forward almost exactly the same idea decades earlier, and the core model is essentially Sewall Wright’s mainland island model of population genetics with the word “species” inserted for “allele”. Hubbell’s neutral theory is another example, and the origin in both cases is other theories/ideas that are molded into something new (in subtle ways or major ways, depending on your point of view).
In terms of empirical studies:
(3) The first clear test of a major theory. Simberloff and Wilson’s experimental test of island biogeography theory using teeny mangrove islands blasted with insecticide comes to mind. What are other good examples? Here, one might think of the new “idea” involving the choice of system, and the origin of the idea seems clearly to be a search for ways to test an existing idea/theory.
(4) The biggest, best test of a major theory. Tilman’s massive biodiversity-ecosystem function experiment in the field comes to mind. Others? Again, to the extent that this constitutes a novel idea, the origin is also clearly traceable to existing theory.
To come full circle, it was humbling for me to realize somewhere during the middle of sabbatical that I was in the process of spending an entire year writing a book based on an idea that was planted in my head 20 years earlier, the very first time I dabbled in ecological research. I suppose the moral of the story would be to always keep your ears and eyes open – you never know from where and when an idea will arise that guides the coming decades of your research life. (That for sure is not a novel idea, but one worth thinking about!)
Great post! I found this stimulating and will keep mulling it over as my day goes on. It is interesting to see what papers ecologists/evolutionary biologists see as “new”- glad to recognize some of them! I posted a parallel take on this theme on my blog a short while ago, with a focus on the “value” of ideas. http://whatsinjohnsfreezer.com/2016/01/17/ideas/ An undercurrent there of lamentation(?) about how it’s harder to have new ideas today in science (in my fields anyway), perhaps.
The longer I am around I increasingly think there is truly nothing new under the sun. Ideas always have precedent. I don’t think ecology has ever had or ever will have an Einstein. For that matter, I’m not sure physics had an Einstein or just a myth of Einstein. It is quite true that he wrote 4 papers in one year, each worthy of a Nobel prize while working in the patent office. But all of them were in areas of active discussion and building on the empirical results of others. And he had just finishing his PhD and wasn’t as intellectually isolated as people like to make out. Even Einstein’s theory of specialty relativity was more an explanation of the Lorenz contraction formulas that had already been published by two independent developers over a decade previously.
I tend to think ideas are “in the air” and that somebody in the community is going to pull it out of the air. At the point it is more a matter of timing who pulls it out of the air. The Darwin-Wallace story fits this model.
Thus novelty is primarily in:
1) Timing – emphasizing something when the field is ready for it
2) Communication quality – espousing an idea clearly
3) Recombination – remixing existing ideas in a way that captures people’s attention
4) Degree – first empirical test of other person idea. Bigger test.
5) Luck – being the person who pulls the idea out of the air 6 months before somebody else would do it
About your experiences with your original paper. My adviser, who was also an Editor in Chief of Evolutionary Ecology Research always said that when reviewers say an idea is obvious without citing literature of where it is already published, then that is a sign that it is a really important paper.
Re: Darwin’s originality, Peter Bowler would disagree with you (but it’s a debatable point):
“when reviewers say an idea is obvious without citing literature of where it is already published, then that is a sign that it is a really important paper.”
Interesting remark. Will have to mull that over. My gut feeling is that it might be true, so I’m trying to recall any counterexamples from my own experience.
Thanks, Brian. I think it is really important to mix into the discussion random factors like timing and luck. Even communication quality could be seen as having an element of chance (you could have a fantastic idea but not the luck of slick communication skills). This reminds me of Malcolm Gladwell’s book “Outliers”, in which a huge emphasis is on luck, timing, and hard work, in addition to smarts when it comes to major innovations.
Even if the Einstein story isn’t quite right, it’s such a good story! How about isolated mathematicians who solve age-old proofs?
” How about isolated mathematicians who solve age-old proofs?”
Yeah, my impression from reading popular math books is that those are some of the best examples of true novelty. Andrew Wiles of course drew on existing techniques and ideas to provide Fermat’s Last Theorem. But he worked on it in secret, and nobody but him had any idea that the approach he eventually hit on would work.
Sorry to be late to the party…
I was going to mention Brian’s #2 and #3 (and I like the other three but didn’t think of them). In particular, I think there’s a lot of innovation in borrowing ideas from other disciplines or subdisciplines or even study systems. I find it fascinating that ecologists tend to study totally different questions in different systems. I’ve wondered, for example, about why we don’t do the equivalent of 50-ha tropical forest plots in diverse grassland systems. Similarly, I have several times either come up with or talked with someone else developing techniques I then discovered were already pretty sophisticated in another field (epidemiology, computer science, etc.)
Thanks, John. I enjoyed your post – I like the line about debating “which hairs have been split and by whom and when”.
Is it harder to “have new ideas today in science”, compared to some earlier time? Interesting question. I’m not sure that’s really true. I’ll imagine that it’s always felt hard to come up with new ideas, except perhaps during short periods up conceptual upheaval, the same way that “kids today…” never seem as good as the kids of yesterday (i.e., us!).
I also wonder whether the fact that many ideas seem obvious in retrospect contributes to the feeling that it’s hard to come up with a new idea. That is, we think that everything obvious must have been noticed already, so if past ideas seem obvious, there must be nothing left!
Thanks Mark! I’ve long thought that, as knowledge accumulates, making “big leaps” in knowledge becomes harder and science becomes more incremental (or some fields even die out, or are seen to; e.g. anatomy is often seen that way by non-anatomist scientists, post-1950s). I have even felt that in my own career… but that might only be me. 🙂 Just a gut feeling, but maybe some science historians have hard data that have already tested that?
Interesting. About possibility (1), maybe the flow of ideas is always more gradual than popular stories would have us believe. If I am not mistaken, one of the main activities of the patent office where Einstein was employed was to review electromagnetic devices that synchronize clocks over large distances. That doesn’t change anything to Einstein’s greatness, but it makes sense to be preoccupied by the notion of time in a place where synchronizing it is a key issue.
Concerning category 1, how about: George Price’s equation; particulate inheritance after Mendel’s observations.
Re: Price, Robertson independently hit on a special case shortly before Price came up with the general equation, so it’s sometimes called the Price-Robertson equation. But yeah, I’d say Price was pretty original. And in a variant on a phenomenon Brian referred to above, Dick Lewontin initially dismissed the Price equation as trivially obvious when Price first wrote to him about it. Lewontin later changed his mind and apologized to Price for failing to appreciate the Price equation initially.
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