Making ideas or evaluating them? Climbing aboard theoretical bandwagons


It’s no mere coincidence that both Darwin and Wallace figured out natural selection at roughly the same time. The basic facts at the foundation of the mechanism of natural selection seem to have been established for a couple millennia. They didn’t converge until the Victorian era of natural philosophers. Before that time, some false assumptions about the nature of existence stood in the way.

In a similar vein, both Newton and Leibniz independently developed calculus at the same time as one another.

Likewise, Verhulst created the logistic equation. Then, it took almost 100 years for someone to come upon this again, by Pearl and by Lotka who did this independently of one another.

At the start of the 1900s, people were attempting to build a heavier-than-air machine capable of controlled flight. There was a convergence of technology and ideas that allowed these things to develop on three continents, at just about the same moment in human history. That’s no mere coincidence. History was ripe for that to happen, though it took a special vision, and plenty of hard work applied in just the right way, to put things together. The Wright Brothers were were perpetual tinkerers. They were also driven by data, experimentation and critical analysis of their findings, allowing them to figure out the actually fatal errors of their predecessors. (It’s worth a visit to Dayton, I had the chance to visit a couple months ago. Their bicycle shop looks and feels a lot like a lab you’d find at a small teaching school. It’s mighty inspiring.)

For every Darwin and Newton, whose ideas had contemporary shadows, there are many more innovators that go it alone. If their ideas were not developed, then we have to wonder if they ever would have happened. Some people say that about the smartphone. It’s hard to say how often this is true. Regardless, there is a reward to the first to figure out an important idea, when these ideas spur progress. (I have to admit that the copy of Kuhn’s Structure of Scientific Revolutions on my shelf is dusty and not fully read. I think more people have made it through Ulysses.)

I got to take a vacation to Iceland a couple years ago. It was enlightening. And there was a Penis Museum in Húsavík, too. For a millennium, Iceland’s subsistence living, and whatever mediocre export economy that could be mustered, depended heavily on sheep. While farmers in Europe were using the spinning wheel for centuries, Icelandic farmers were still spinning wool with feeble handspools. Moreover, back in the day they made shoes out of hide, but never figured out how to make leather. A long journey would require several pairs of shoes for long journeys because they would wear out so quickly. Some contemporary roads are named after the number of pairs of shoes it used to take to make the journey along the road. I don’t mean to pick on the Viking ancestors of contemporary Icelanders, as they withstood the little ice age far better than I ever could have. I don’t know if, while spinning wool on a handspool, I would have been the one to independently invent a spinning wheel separate from outside influence. I’d like to think I could have been that resourceful, though I might have been too busy to take the days off to work on it.

As contemporary Icelanders can tell you, the development of new ideas matters.

Orville and Wilbur Wright invented the plane. Now, without consulting Wikipedia, can you tell me who else was critical in the development of early airplanes?

Many people did great and important work on early flight. Their contributions were critical, even if we can’t recall many of their names. Heck, I’ve been surrounded by aviation history for more than a decade (on account of my spouse’s job and the location of my campus) and I can’t name more than a handful of the pioneers of early flight.

from wikimedia commons

from Wikimedia Commons

Here’s why we can’t remember those other guys (and, it seems they indeed were all men) who turned early planes into something workable for society: their jobs were interchangeable.

I posit that anybody with the training in engineering, math and workmanship skills could have followed through on the first principles developed by the Wright Brothers to grow the field of aviation. Much of it was done by the Wrights themselves, but they had many colleagues and competitors. Flight wouldn’t have taken off (heh heh) unless there was the labor and brain juice expended by many people at the time.

When a new idea comes out, which is more important, the development of the idea or the fleshing out of the idea? Clearly, more glory comes with the former. Both are important. I think it’s silly to say that one is more important than the other because both are essential components. When a great idea comes around, someone’s got to put meat on those bones. It take a whole community of researchers to do that.

For example, some have said that E.O. Wilson is one of the most important scientists of the past century. Why do people say that? Because he created the kernels of many ideas. He put them out into the world, and then many people pursued them. These include the taxon cycle, island biogeography, the social regulation of caste in social insects, sociobiology. He fleshed out the ideas enough to get others to test them out in great detail. He never really lingered on these ideas once he put them out there.

The community of scientists is principally composed of people who are testing theories and fleshing them out. After someone figured out the spinning wheel, then there were many people who worked on the design to make it better. That task of filling-in-the-details is the currently bulk of work in science.

Humor me while I bring out a couple more examples.

In the field of ecology, Hubbell’s formulation of neutral theory was a major progress as a null model that was entirely lacking in community ecology. In the field of behavior, Hamilton’s conception of inclusive fitness revolutionized how we think about the evolution of social groups. After these ideas were formalized, small armies of researchers have pursued these questions to hammer out details, question theoretical foundations, and understand how things can be generalized and how things might not occur. Regardless of how significant kin selection is 100 years from now (I am not invested into it either way), the formulation of the idea by Hamilton was successful in spurring a scientific revolution, which is still spinning to this day (and Wilson even stepped into the fray as a gadfly).

Many of my friends and colleagues have done great work, with much of their careers invested, on the details of kin selection and many of its subtheories and corollaries. So, I hope I don’t hurt any feelings when I suggest the idea that a lot of this work could have been done by interchangeable scientists. (I’m open to being convinced otherwise.) The work required brilliance, perseverance and specialized training. However, if any one person didn’t make some of the contributions, then the gaps would have filled in by the others. As a group, the entire endeavor was significant and as a community, researchers of social animals learned a ton. I greatly value their contributions, and some of them are a model for how I run my own lab in a number of ways.

Who should be a part of that workforce ? Does it matter? Who is best suited to it?

Who is suited to making big new concepts, and who is suited to that kind of fleshing-out-of-ideas science, to test existing theories, and build upon these to make new subtheories? Moreover, what kinds of research labs are suited to each kind of option? My little undergraduate lab probably shouldn’t follow the same path of a lab with multiple doctoral students and postdocs.

So, I don’t choose that path.  I mean: I don’t like either option. I choose option C.

What’s option C? That requires a taxonomy of research goals. That’s a set of posts within the next month.

13 thoughts on “Making ideas or evaluating them? Climbing aboard theoretical bandwagons

  1. Nice post, with a nice range of examples.

    Darwin himself ended up with the lion’s share of credit for evolution by natural selection (even Wallace agreed and gave Darwin the credit!) not primarily because he did in fact come up with the basic idea before Wallace did, but because he developed it much more fully than Wallace. Darwin’s the one who worked out all the implications and lined up all the relevant evidence from animal husbandry, paleontology, biogeography, embryology, taxonomy, geology, etc.

    Re: Hubbell’s neutral theory, it’s interesting to note that Hal Caswell proposed a version of the same idea in a paper in 1976, and that around the same time as Hubbell was first publishing, Graham Bell was publishing a version of the same idea. I hear that Hubbell himself says that he has no idea why “neutral theory” in ecology seems to be identified with him exclusively, and not also (or instead) Caswell or Bell. After all, all three were very famous, all three published in very prominent venues, and all three made many of the same points (e.g., neutral models as null models, neutral models as making predictions about many different interesting patterns in ecology).

    Of course, the fact that neutral theory was already well-developed in evolutionary biology for decades before any of those guys wrote is another issue. Historians often talk metaphorically about how ideas like evolution by natural selection must’ve been “in the air” in Darwin and Wallace’s time, given that they both hit on the same idea independently and for some of the same reasons (e.g., both had read Malthus). But in the case of neutral theory, the idea wasn’t just metaphorically “in the air” but literally on the page, in the work of people like Wright and Kimura. Indeed, Hubbell’s own version of neutral theory is just a reinterpretation of a previously-existing population genetics model. I note this not as a criticism at all, but just to highlight how the idea was already out there and already fully developed, it was just a matter of recognizing its relevance for ecology.

    And regarding your larger point, I agree with you. Most science that gets done, could’ve been done by lots of people besides the person who did it (and also doesn’t materially affect the direction of the field whether it gets done or not). I have an old post that makes a semi-related point, that big but flawed ideas (like the intermediate disturbance hypothesis) shouldn’t be given “extra credit” by saying “well, the idea was flawed, but at least it led to lots of good research”. Because, had the flawed idea not been proposed, lots of good research (by which I mean, the ordinary sort of anyone-could-have-done-this research) would’ve been done on *other* topics instead, under the influence of other (possibly non-flawed) big ideas. Flawed ideas generally don’t increase the *total amount* of science that gets done, they just cause *different* science to be done than would have been done had the flawed idea never been proposed. Now of course, often the only way to find out that an idea is flawed is to pursue it, which is fine. I’m just saying that, after an influential idea is discovered to be flawed, that it doesn’t make any sense to talk about its influence as if that somehow *compensates* for the fact that it turned out to be flawed. What we should say is “It’s too bad that that idea turned out to be a dead end, and that it took us all that time and effort to figure out that it’s a dead end.” Just because it’s not possible to avoid ever exploring dead ends doesn’t mean we should be *happy* when we discover that we’re exploring a dead end.

  2. Amen. Every 30 years, the same ideas pop up again and again. People weren’t ready to think about community assembly as a neutral phenomenon, even as a null model, before his time. Just like people weren’t ready for genetics without understanding selection. It’s funny, nowadays, I bet the person who uncovered Mendel’s work would get all of the credit instead of Mendel. I don’t know who it was, offhand. I think Hubbell got the reputation for neutral theory in part because of timing, but also it was the culmination of a lot of his work on a system that is broadly found to be puzzling, the richness of tropical forests. But maybe I think that because I’m a rainforest guy.

    (And, you’ve half-written my post for next week and the following! The part about research being poured down the drain of flawed bandwagons, and how to avoid that. Or at least how I try.)

  3. That (and subsequent links) were interesting reads. So, de Vries at first didn’t even mention Mendel until he was called out on it by other botanists who knew that he knew about it.

    Wikipedia is awesome. To my knowledge, it’s yet to fail me. (That is a big qualifier, though.)

    • And the Brazilians and the French also make some substantial claims at being first, too. Like the Darwin/Wallace situation, who came first isn’t as prominent as who was more comprehensive. I’m less of an expert on early flight, but those other claims aren’t as nearly well backed up as the Wrights, who arranged for witnesses and had full engineering diagrams of their work.

  4. I think that the faceless nature of most science is its greatest strength. Thankfully, in many cases, it is history that gets to assign credit, overriding the perspectives of contemporary researchers. And sometimes what starts out as “workaday” science (Mendel’s experiments were not exactly the large hadron collider!) can end up forming a theoretical cornerstone for an entire discipline. My point, I guess, is that the exciting thing about science is that you DON’T KNOW where it is going to lead, AND almost anyone with the inclination and a modicum of intellectual discipline can contribute to it meaningfully. Here’s to being one of the faceless!

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