Note from Jeremy: this is a guest post from Peter Adler.
In my view, the current culture of ecology suffers from an unhealthy obsession with novelty and a problem with conceptual fragmentation. I suspect these are related problems linked in a positive feedback cycle.
First, to illustrate what I consider our unhealthy obsession with novelty, here is an excerpt from a recent review of one of my manuscripts: “…the only negative thing I can say about this paper is that it comes across as rather confirmatory in nature. It is absolutely solid science and highly interesting and important but the writing does not punch you with novelty.” Our paper was eventually accepted after we made a stronger case for its novelty, so this isn’t sour grapes. I’m quoting the review because I think it perfectly captures the current priorities of our field: to get a paper into a top-tier journal, or a grant funded at NSF, it’s not enough for the research to be solid, interesting and important. It also has to be novel.
To give a more specific example, in one of my research areas, coexistence, it feels easier to publish theoretical “what if?” papers about intransitive loops and higher order interactions than empirical papers quantifying the strength of the pairwise interactions we’ve thought about for decades, but still struggle to rigorously measure. Similarly, I would bet that a proposal about a sexy new concept/interaction/process that has a small chance of being an important driver of dynamics has a better chance of being funded than a proposal to do the tedious work of carefully measuring effects of the long-recognized drivers we know are important (e.g. drought in water limited ecosystems). As my colleague Steve Ellner likes to say, “NSF is interested in questions not answers.”
The conceptual fragmentation problem was the motivation for Mark Vellend’s recent book, and leads to papers listing the 100 most important research questions in ecology. Can we really expect our poorly funded discipline to make progress on so many questions? Having too many priorities is effectively the same as having no priorities.
The Long-Term Ecological Research network provides another case in point. Despite being a coordinated, national program with a fairly applied mission statement (“to provide the scientific community, policy makers, and society with the knowledge and predictive understanding necessary to conserve, protect, and manage the nation’s ecosystems, their biodiversity, and the services they provide”), every LTER site comes up with its own conceptual framework, and collectively they span much of the bewildering variety of ecological research. Contrast that with NSF’s Critical Zone Observatories, which have an even broader mission (to “discover how Earth’s living skin is structured, evolves, and provides critical functions that sustain life”), but, in my very limited experience, all seem to focus on similar questions about carbon and water cycling and don’t have a problem spending big money to get a better estimate of one important flux.
Why do I think novelty and conceptual fragmentation are related? Pressure to demonstrate novelty creates a perverse incentive to minimize connections with previous work. In Vellend’s language, the incentive is to emphasize the uniqueness of low-level concepts and individual case studies, rather than the unifying commonalities of high-level concepts. This is a recipe for a discipline that cannot agree on its priorities. With everyone working to promote their own pet idea, rallying around a few grand challenges becomes impossible.
At the same time, if we can’t agree on what is important, then by default novelty becomes the key criteria for evaluating papers and proposals. At least we can agree on what is new, right? It’s much easier to recommend rejection because a paper isn’t novel than to make a difficult and seemingly more value-laden argument about why it is not important.
The irony of this predicament is that collective action itself becomes a novelty. I’m thinking of the Nutrient Network and similar distributed research efforts. When dozens of ecologists agree to pursue a few core questions using consistent protocols, you get novel (and important!) results that get published in top journals. Choosing and agreeing on those core questions is the hard part, agreeing on consistent methodology is secondary.
So why do I care? After all, I’ve done fine under the status quo. But I am increasingly concerned about future funding for basic research. I’m becoming more convinced that we can’t expect society to support ecological research for knowledge’s sake alone. In the long run, our best hope of maintaining funding for basic research may be to show that it can sometimes help solve problems important to society. But an over-emphasis on novelty and our conceptual fragmentation act as barriers to collective action and make it hard to solve big, complex, problems. I’m not suggesting we ignore novelty altogether–we absolutely need to keep incentives for innovation. But I do think we need to reconsider and adjust our priorities. We should publish solid, interesting and important papers in our top journals, even if they don’t punch you with novelty. The challenge in making this shift is reaching some agreement about what is “important”; what are the highest priority problems our discipline should try to solve?