What correct scientific idea hasn’t yet proven fruitful or influential, but will in future?

Scientific ideas can have various virtues. Most obviously, they can be correct. But they can also be clever, surprising, elegant, etc.

One important but difficult-to-pin-down virtue is fruitfulness. A scientific idea is fruitful if it leads to a lot of further research, especially if that research retains long-term value (it wasn’t just a trendy bandwagon or whatever). Fruitfulness overlaps a lot with influence.

Fruitfulness or influence covaries positively with correctness, but not perfectly. It would be nice if the covariance were perfect. It’s unfortunate when an influential idea turns out to be wrong, because the work that grew out of that idea often loses at least some of its value, and because there’s an unavoidable opportunity cost to building on ideas that turn out to be wrong. Andrew Hendry has a compilation of ecological and evolutionary ideas that inspired a lot of research despite being (in Andrew’s view) wrong, or at least not all that important.

In this post I’m interested in the flip side of incorrect-but-influential ideas: ideas that were correct but not influential. Somebody said something true–but nobody else cared. Correct but non-influential ideas are the proverbial tree falling in a forest that doesn’t make a sound.

What are your favorite examples of correct-but-uninfluential ideas in ecology? In all of science?

The most obvious examples of correct-but-uninfluential scientific results are those that are true but boring, because they’re trivially obvious or lack any broader implications (e.g., reports of the first record of species X in locale Y). Let’s not bother compiling such examples. I’m more interested in ideas that haven’t (yet) proven fruitful or influential even though there’s some good reason to think they could have been or should have been. Also, recently-proposed ideas don’t count; they haven’t yet had enough time to become influential.

In an old linkfest we talked about “Sleeping Beauties”, papers that were little-cited for many years before suddenly becoming influential. Price (1970) is an example from evolutionary biology. Moran (1953) is an example from ecology. The recent explosion of interest in modern coexistence theory is another example from ecology. Metropolis et al. (1953) is an example from computing. What I’m looking for are suggestions for papers that might yet become (or that in your view deserve to become) “Sleeping Beauties”–papers that haven’t yet inspired much research despite ample time to do so, but that should or will do so in future. Sleeping Beauties that are still asleep, as it were.

Looking at those examples of Sleeping Beauties suggest some hypotheses for what prevents correct ideas from inspiring as much research as they should. One is that the idea is difficult to understand. That’s surely at least part of why it took interest in the Price equation and modern coexistence theory so long to take off. Interest in such ideas only takes off after they become widely-understood, often because someone comes along who’s very good at explaining the idea. I’m thinking for instance of Steven Frank’s work explaining the Price equation to other evolutionary biologists, which not coincidentally coincided with a jump in interest in the Price equation. Another is that the most obvious “next steps” are infeasible. For instance, I wonder if that’s part of why interest in the “Moran effect” took so long to take off–back in 1953 there wasn’t much long-term spatial data on population dynamics and weather variables with which to do the most obvious tests for the Moran effect. I also wonder if that’s why interest in Metropolis (1953) took decades to take off–we lacked the computing power to implement the idea (right?) A third reason why a correct idea might remain uninfluential is that it was published in an obscure venue.

So here’s a “search image” for Sleeping Beauties that are still asleep: find a correct but difficult-to-understand idea that’s been around for a while, but has just recently been well-explained to a broad audience by a paper or book that’s likely to be widely read. Here’s a second search image: an idea that is correct and that everyone’s interested in in principle, but that we currently lack the technology to implement or have only recently acquired the technology to implement. What uninfluential ecological idea is about to become influential now that drones and citizen science are things? Are there any uninfluential ecological ideas that are about to become influential because they help us understand the microbiome?

Looking forward to your predictions. Then we can revisit this post in a decade and see who turned out to be right! 🙂

p.s. Correct-but-uninfluential ideas have a close connection to incorrect-but-influential ideas. Stephen Heard suggests that the question of whether insect herbivores regulate plant populations is an important question ecologists should be asking. But they’re not asking it because they think, incorrectly in Stephen’s view, that the answer is obviously “no”. In this case, the possibly-correct idea is uninfluential because the possibly-incorrect converse of that idea is influential.

8 thoughts on “What correct scientific idea hasn’t yet proven fruitful or influential, but will in future?

  1. Here’s a non-ecological candidate: room-temperature superconductivity. It was a hot thing for a little while, but my impression is it ceased to be hot because materials that superconduct at near-room temperature are ceramics that can’t be formed into wires or electronic devices. If anyone ever solves that problem, room-temperature superconductivity will be hot again.

  2. Maybe not quite an idea that has had time to be overlooked- but I think perhaps one that is hanging in the weeds for now, but has the potential to blossom into something quite big in terms of attracting future research: ONCE.

    Organic Nonoptimal Constrained Evolution (ONCE)- which, in a nutshell proposes organisms contribute to the formation of their niche spaces and therefore are the central force of their evolutionary history (Diogo R., Frontiers in Ecology & Evolution, Feb 2017).

  3. Ooh, here’s a good candidate: quasi-potentials as an alternative to local linear stability analysis. The idea goes back to the 1970s, but was never pursued because there was no general, practical numerical method for computing quasi-potentials. Now there is, and it’s been implemented in an R package and plugged in a prominent venue (Nolting & Abbott 2016 Ecology). Ok, that’s my pick for an ecological Sleeping Beauty that’s about to wake up.

    • Wow! It is a huge honor to be mentioned here. Thank you!

      I’m excited about the future of quasi-potentials in ecology. The concept is gaining traction in evolutionary theory. Xu and Wang have a paper that will be appearing in the Journal of Theoretical Biology soon. It uses quasi-potentials, and is called “Quantifying the potential and flux landscapes of multi-locus evolution”. I’m really looking forward to reading it when it comes out!

      Thanks again!

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