Like everyone else, I’ve written the paragraph about how the research I’d like to have funded is “innovative”. I’ve had to: over and over again, we see agencies listing “innovative” as a criterion for funding. Heck, it’s even in the name of two funding agencies from which I’ve had money in the past: the Canada Foundation for Innovation and the New Brunswick Innovation Foundation.*

Like a lot of things, the idea that science should be innovative is very appealing – as long as you don’t think very hard about it. If we did do some thinking, I hope we’d stop using whether work is “innovative” as a criterion for funding. It’s not helping us; in fact, it’s actively harmful.**

It’s not that I’m opposed to innovation; some of my own work has been innovative. What turned out to be (I think) my most influential paper (this one, on the shapes of phylogenetic trees and how they measure among-lineage variation in speciation and extinction rates) was pretty novel when it was published. (Mind you, that was mostly by accident.) Of course, innovation doesn’t always mean influence. This paper (about how travel costs for ovipositing insects might help stabilize plant-insect systems) has been pretty much ignored, and I think that’s partly because it was simply too innovative. I know, that sounds like absolutely classic self-serving self-delusion, so if you’re skeptical, consider my argument here.

So yes, I can do innovation. But I’ve also produced pretty good work that’s not innovative at all. This paper (which asks whether there’s evidence for replicated host-race formation across nine different insect herbivores of goldenrods) takes standard approaches to a familiar question in a well-studied system; it just extended an idea to additional species to take advantage of an opportunity for cross-species comparison. I could go down my CV and pull out plenty of other examples: much of my work just isn’t innovative. And while it might seem that I’m putting myself down, I don’t think I am. Because we need a lot more uninnovative science. At least, we do in my own field (ecology and evolution).

What’s this uninnovative science we need more of? I could give you a very long list. Let’s start with species descriptions. We share our planet with somewhere between 3 and 300 million other living species (the fact that we don’t even know this number is something of a professional embarrassment). The work of describing and naming these species is absolutely critical for ecology and conservation – how can we understand and preserve the workings of a system if we can’t identify, or even refer to, the elements that make it up? There are certainly innovations to be made in the process of species description (consider the brouhaha over namings from barcoding). And the coining of new Latin names is, as I’ve argued in many places, one of the more creative acts in all of science. But the basic task is intrinsically repetitive, and most useful when it’s not innovative (that is, species descriptions and taxonomic revisions are formulaic for good reason). Again: this is not to denigrate the worth of species discovery as part of science. It’s one of the most important things we need to do – but its funding suffers terribly in part because it’s challenging to pitch it as “innovative”.

I said I could give you a long list. While I’ll spare you that, I won’t stop at just one example either. We need population and biodiversity surveys of more different areas, preferably using the same tools, not different innovative ones each time (because we need to draw comparisons). Even more, we need resurveys, where we monitor populations and biodiversity in the same areas over time. We need studies finding ecological interactions (and other phenomena) in one system to be “replicated” using similar methods in other systems, or in the same system in different places.*** We need meta-analyses of global patterns in diversity, energy flows, carbon cycling, soil microfauna, and much, much more – and those meta-analyses need primary studies to work with, and the job is much harder if each primary study can only be funded if it’s done differently from every other one. We need – no, you’ll be bored soon, I’ll stop.

Innovation is overrated. Sure, an innovative approach can be exciting; sometimes it can crack a hard problem that couldn’t be cracked before. But other times, it gets in the way. Science has a big job to do, and a lot of it just needs us to keep on with what works. We should fund uninnovative science – lots of it. I’m proud of my innovative papers, but I’m proud of my pedestrian papers too.

© Stephen Heard  August 8, 2023

Image: innovation is overrated, CC0 by Simon Cygielski via from Openclipart.org

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*^The New Brunswick Innovation Foundation came along after the Canada Foundation for Innovation already existed, and clearly reversed the order of words in its name because that made its name innovative.

**^I’m not going to write about maybe the most obvious way this is true: work can be innovative and also bad. Sometimes, work is innovative because it’s bad – because sometimes there’s a really good reason nobody has ever done Thing X before. Let’s assume that nobody is funding work only because it’s innovative.

***^“Replicated” is in quotes there, because I think what we need isn’t really what advocates of replication mean, when they talk about the “replication crisis”. True replication plays a rather small role in science, and I suspect always will. I bet that sentence sets some people off.