Here’s a notion: When we discover a big new thing, this often requires an abandonment — or at least serious doubt — of a commonly accepted notion.
I went to a bunch of scientific conferences this summer. Four of ’em. I have a smorgasbord of reflections on the whole experience to share with you.
I was chatting with a friend in a monthly book group. A rare event happened this month: everybody in the group really liked the book. It turns out that that most of the books they read are not well-liked by the group. How does that happen? Well, this is a discriminating group, and there are lot of books on the market; many books aren’t that good.
We speculated about why so many non-good books are sold by publishers. The answer is embedded within the question: those books sell.
Let me overgeneralize and claim that there are two kinds of novels: First, there are those that were brought into the world because the author had a creative vision and really wanted to write the book. Second, there are novels that are written with the purpose of selling and making money. Of course, some visionary works of art also sell well, but many bestselling books aren’t great works of art. (No venn diagram should be required.) Some amazingly great novels don’t sell well, and weren’t created to be sold easily in the marketplace.
Most novels were never intended for greatness. The authors and the publishers know this, but have designed them to be enjoyed and to have the potential to sell well. When someone is shopping for a certain kind of book, then they’ll be able to buy that kind of book. Need a zombie farce? A spy thriller? A late-20s light-hearted romance? I have no problem with people writing and selling books that aren’t great. Books can be a commodity to be manufactured and sold, just like sandwiches or clothing. A book that is designed to sell fits easily fits into a predetermined category, and then does its best to conform to the expectations the category, to deliver to the consumer what was expected.
I think a similar phenomenon happens when we do experiments and write scientific papers.
First, some research happens because the investigators are passionately interested in the science and have a deeply pressing creative urge to solve problems and learn new things.
On the other hand, some research is designed to be sold on the scientific marketplace.
To advance in our careers, we need to sell our science well. The best way to do this, arguably, is to not aspire to do great science. We can sell science by taking the well trod path on theoretical bandwagon, instead of blazing our own paths.
If you want a guarantee that your science will sell well, you need to build your research around questions and theories that are hot at a given moment. If you do a good set of experiments on trendy topic, then you should be able to position your paper well in a well-regarded journal. If you do this a dozen times, then your scientific career is well on its way.
On the other hand, you could choose a topic that you are passionately interested in. You might think that this is an important set of questions that has the potential to be groundbreaking, but you don’t know if other people will feel the same way. You might be choosing to produce research that doesn’t test a theory-of-the-moment, but you think will be of long-term use to researchers in the field for many years to come. However, these kinds of papers might not sell well to high-profile journals.
Just like a novelist attempting to write a great novel instead of one that will sell well, if you are truly attempting to do great science, there is no guarantee that your science will sell. Just like there are all kinds of would-be-great novelists, there are some would-be-great scientists who are not pursuing established theories but are going off in more unexplored directions.
Of course, some science created for the marketplace is also great science, too. But the secrets to creating science that sells, are very different than the secrets to doing great science.
After all, most papers in Science and Nature are easily forgettable, just like the paperbacks for sale at your local chain bookstore.
Update: For the record, y’all, I’m not claiming that I am above doing science to be sold. That’s mostly what I do. I’m just owning that fact. There’s more on this in the comments.
This is the fourth and final post in a series, wherein I attempt to make the case that tinkering is a viable, and perhaps optimal, approach to conducting a research program, particularly for those at teaching-centered institutions. Here are the first, second, and third posts preceding the present post.
I’m a tinkerer. That means that I don’t typically design my research to fit the framework of a big theory, but instead I set out to answer a small little question that has occurred to me. I do experimental research, combined with observational research, to find the answers to open questions. I’m just not going after the big fish that other labs do. After all, I work in a small pond.
This is a personal narrative about how tinkering has worked for me. It’s hard to write about the concept in the abstract, so I’m going into the specifics about one line of tinkering I’ve done over the years. If I am going to make the case that tinkering works well for me, it’s easiest for me to to use specific projects to illustrate how tinkering has worked for me. So if you read on, you’ll be reading about ants. Consider yourself forewarned.
When I started as full-time faculty at a teaching institution, I found myself with the position of having a field season in front of me. What did I want to do?
I quickly decided that I wouldn’t continue along the lines of my dissertation, which was on the biology of invasive ants. There were so many questions about biological invasions that were interesting to me, but they all seemed too, well, big. For all of the specific big questions about invasiveness that I wanted to tackle, there were other labs that were going at it at the same time, full time with multiple collaborators, without teaching. (In the end, their work was — and still is — awesome in its creativity and quality, going well beyond my initial interests. In my position, I don’t think I ever could have run most of the experiments they have, at least not on the scale that they did. I admire their work a lot.)
My dissertation was one part of getting the invasive ant bandwagon rolling, but after taking a job at a teaching institution, I needed to find a better ride. I had a few papers that made a difference, by looking at the issue from a broader-than-usual perspective, and it was time to move on.
I knew that I wanted to get back to my field station in Costa Rica. It was a place that I knew well from my dissertation, and it had become kind of a second home to me, and I hadn’t been down there for 18 months. I had a few weeks on site, along with several undergraduate field assistants.
I wanted to pick a project that fit three criteria:
- The project could be completed in a few weeks
- The project lead to a modest publication, regardless of what the results were
- It would be fun
Here was my thought process: This rainforest is chock-full of ants, everywhere. People study them all of the time. But they only study the cool and bizarre ones, like leafcutters, bullet ants, ant-plant mutualists, and army ants. There are hundreds of ants that make the forest run that are overlooked. I wanted to study one of those. So, I picked what I thought what was one of the most common, but unknown, species, and designed a cute little project around it. (By the way, free versions of all the papers in this post are found on my website.)
My main goal was to ask, “What is up with this extremely common species that we know nothing about?” I built it around a question about unpredictable resource heterogeneity, competition, and whatnot, but it was mostly a vehicle to play around, because I knew nothing about this species. And I wasn’t going to go down for a few weeks and not get a paper out of it.
Even though I designed that cute little project to be fail-proof (negative results would still be publishable), I barely eeked that paper out. That was because my sample size was dropping precipitously throughout the short experiment. We started out by marking a bunch of colonies in the field. As days progressed, the colonies flat out disappeared. Their nests were just empty holes. By the end of our experiment, we sorted out that they just moved nextdoor. Over the course of a few weeks, we’d lost well more than half of our colonies, but I didn’t have data on them after they moved.
The next field season — one year later, after my first year on the tenure track — I had a few more weeks with a team of undergrads. I wanted to understand the non-optimality of home range size. I was ready for nest movements, and built it into the experimental design. The answer was kind of interesting: foragers spent more time looking for food before giving up when the home range is of poor quality.
At this point, for two years on the tenure-track teaching a full courseload of new courses, I’ve gotten two okay papers out from two short field projects, while spending time on other projects as well. At the rate of a paper a year, I would’ve been well exceeding scholarly expectations at my university, as a decent first-authored paper per year is pretty good at a teaching institution with a heavy teaching load. I was okay with my publication rate, but I felt like I wasn’t taking this anywhere interesting.
I felt that I knew this critter pretty well. The most curious thing was nest movement behavior. Delving into the literature on nest movements in ants, I found that nest movements have been documented aplenty. But in each species, it was studied only once. It looked like everyone experienced what I did – they stumbled on the phenomenon which botched an experiment, and then they wrote up how the experiment was botched by nest movements. Then, they moved onto more tractable systems, using animals that don’t disappear when you’re not looking. Nobody had gotten far beyond the nest-movements-botched-my-study study.
I decided to directly tackle nest movements in my next field season, which was, again, with several undergrads for about a month. All I wanted to know was, “why do they move their nests all the time?” You can’t ask “why” questions with science, though, so I asked “how” and “with what consequences, correlates and a potential cause.” These results were really interesting to me. It turns out that they move, on average, about once per week, and it has nothing to do with food or competition.
After working on a variety of other things, I wanted to take some time to get back to these mysterious nest-moving ants. My earlier work suggested – only vaguely – that odors might play a role in how they move their nests. I wanted to see if this was the case. So, I ran an experiment by experimentally manipulating nest odors. It turns out that nest odors can keep them from occupying or staying in nests, but the manipulation had enough artifacts I can’t really trust that this experiment explained what was really happening.
While working on other stuff, this nest odor problem kept nagging at me. Eventually, while I had students doing a variety of other things, I cooked up a field manipulation for myself to run, by reducing odors within the nest. That made them like their nests more than they would otherwise. But then, again, what does this really show? If their endogenous odors make them dislike their nests, what’s the selective pressure behind nest movement? That’s a really hard question to address.
That was a few years ago. I’ve just returned to it last year. With one student student, I have (meaning, she has) rerun the earlier odor manipulation, but with narrow chemical fractions to identify which compounds are playing a role. We also have additional observational work happening to test some newer hypotheses. These projects are involving a chemical ecologist who I brought into this project, as I lack any of that mojo, as well as the equipment. (Sometimes not having the equipment is a good thing, I’ve already argued.)
All of these studies essentially have been a set of little side projects, that in all have amounted to a substantial line of investigation over the years. We know more about the ecology of nest relocation in this species, than any other. By the way, their name is Aphaenogaster araneoides. I eventually worked up a new official common name, “gypsy ant.” (That was Anna Himler’s idea.)
How were those experiments tinkering? Well, one thing you may or may not have noticed is that the only reason I did these experiments was to figure out what’s going on with these ants. I was curious about what they were doing, and so I tried to sort it out. I didn’t come in to working with this system with a big question about optimal foraging, neighborhood competition, or social organization in mind. I just wanted to know exactly what this one species was doing, because it was a mystery to me.
Because I was open to this species to telling me what it wanted to, I let it take me in the direction where I was led. You’re moving your nests all the time? Sure, I’ll try to figure that out. I wasn’t setting out to use nest relocation to evaluate any grand theory about social insect behavior or movement theory in ecology. I just wanted to know about what was causing them to move their nests.
In the process, I documented in some detail how they maintain multiple unoccupied nests, but only use one at a time. This was seen in a few other species, but it was a distinct and heretofore undescribed pattern of nesting. I thought to give it a new name — “serial monodomy” — which might stick. What else do you do when you find something that happens that doesn’t have a name?
This project has gotten me to think more about nest relocation in ants. It’s permeated a lot of my thinking about the biology of this community of ants, and has seeped over into my community-level work. I realized that nest relocation is biologically significant, and is not taken into account in so many studies. And we pick our study systems by focusing on the tractable species: those that don’t move. Looking at what is known, I found that most species are apparently mobile, and those are the ones that we don’t study for this reason. Our whole understanding about ants is very biased. I decided to write a review about that idea.
Ultimately, I think my work on nest movements on ants has had some influence on how our research community thinks about ant ecology. At least there’s been some movement (yes, that’s a pun) in that direction. Not too long ago, the prevailing notion was that typical ant colonies are like plants, that just don’t move. There are some oddballs, like invasive species and army ants, that move around, but everyone else is anchored down.
I’m pointing out to others that this notion is false. I’ve only done work addressing nest relocation with this one species, but in the process I’ve called attention to all of those other species that have been found to do similar things but are overlooked.
Of course, anybody who really knows ants easily realizes that nest relocation happens in a bunch of species. But this fact hasn’t been broadly appreciated, nor had it been documented. By working on this phenomenon, in detail, within one species, I was given the perspective that allowed me to make this concept more tangible across the phylogeny.
If you asked me after I finished my dissertation, what are you going to work on? I never would have said, “nest relocation.” I wouldn’t have identified any major concept or theory. I mostly was focused on teaching, after all. I wanted to do some cool projects when I had the chance. This brought me to working with a very common ant, which compelled me to figure out its nest movements because that’s a basic part of its biology. I was just tinkering around with it to figure it out, that’s all. But following that direction, once in a while over the years, I’ve built together a set of substantial ideas, that I imagine will continue to matter for some time to come.
This work on nest relocation on ants isn’t earth-shattering. But it is changing, just a little bit, how we think about ants, including changing some long-held and mistaken assumptions. This is just the result of five trips to the rainforest for 2.5-5 weeks each, over the last 13 years. That’s not too bad.
I think if I went down to the rainforest trying to test a big theory, I would have come back empty handed, or with a few papers that mostly would be collecting dust by now. But simply by wandering off without a specific vision of big theories, I think I’ve done something that results in tangible, if not big, progress.
So, that’s my case for why tinkering is a good way to do science. You might stumble on something amazing, or you might come upon something just mildly curious, but no matter what happens, you’ll learn something genuinely new.
Just imagine what else we’d be learning if other scientists doing basic research, in all kinds of disciplines, started doing research in obscure directions on things that were mysterious to them but didn’t seem of much obvious consequence. I think we’d be learning a lot more about the world and probably develop many new ideas more quickly than we are now.
On my desktop sits a file, as a reminder. It’s the log of a Skype text chat dated 24 October 2007.
My desktop isn’t usually tidy, but this file always sits there in a corner. I haven’t read it in years, but its existence is, in itself, a reminder.
This article is third in a series of four. A couple weeks ago I wrote about whether or not we should try to develop new theories or to test existing ones by hopping on theoretical bandwagons.
Last week I wrote why theoretical bandwagons are good for, or at least well suited to, big labs and that small labs should avoid them. (You might want to read those over, if you haven’t yet, before reading the present post. Or not. Your call.)
This week, I’m explaining the kind of research that I choose to do in my own small lab.
This chat took place with a deep friend of mine as we both were undergoing career transitions, both of us starting out in new (and radically different) faculty positions. (It’s great when your friends are your role models, and when your role models are your friends, even if you only see one another in a long while. It’s not too often that you connect with others whose values and priorities are well calibrated to match your own, and it’s a pleasant confluence.)
I had just moved to a new position, back to my hometown. This change involved a massive shift in pretty much everything. I was wondering what kind of questions I should be pursuing, and how I should go about it. My friend was settling into a tenure-track position at a research institution and his lab was growing exponentially.
We were wondering what I was going to work on next. At this point, I wasn’t sure. I had a number of big questions that I wanted to tackle, each of which would involve a major direction for my lab. Up until this point, I had been doing a series of one-off projects (which essentially is what my dissertation was as well).
So, I threw out a bunch of ideas. I want to work on X, I want to work on Y, and Z looks interesting too. I said I didn’t want my work to get lost as ephemera, addressing theories-of-the moment.
Then, at the same moment, we independently stumbled on the term that describes the work that I enjoy most, and also has had the greatest impact.
My best work has happened whenever I’ve found some little natural history curiosity that has piqued my interest, and then I designed an experiment (observational or manipulative) to tinker around with the system to figure out what’s going on. It was my doctoral advisor who first introduced me to “experimental natural history.” (Sorry about the paywall, damn JSTOR)
This leads to both the stuff that is most cool, interesting, and in the long term useful to other people. I think that good science happened because my approach was most likely to lead to discovery, even if discovery was not the goal.
Research is supposed to result in new knowledge.
What are the odds that you’re going to make a big discovery or formulate a grand theory as long as you’re working on the same ideas that other people are? How much are you pushing the frontiers of science when there are other people out there doing the same thing? If you’re working for a specific applied aim – an HIV vaccine, cancer prevention, et cetera, then I can understand that a massive push in one direction, like against a two-ton piece of stone, is what can make the stone move.
I’m not in the business of inventing vaccines for rapidly evolving viruses or building pyramids. I’m doing basic research. I’m just trying to understand how the world works. There is so little that is known, that I want to mine into directions that that are entirely mysterious. The world is still fundamentally mysterious.
I posit that there are two distinct philosophies that scientists have about the nature of our knowledge, with little middle ground. On one side are people who think that we have learned a lot in the fields that we have studied, and that research is filling in the gaps and discovering new fields that we have yet to understand. On the other side are people who think that we are still vastly ignorant about the world, and even the things that we have studied really heavily remain mysterious and what we think we know may in fact be wrong.
Is this a fair dichotomy? Does one of these describe you or do you fit in the middle somewhere?
I’m in the latter group (or at one end of the spectrum if it’s not a dichotomy). I suspect that a number of ecologists might fall into that group as well. For all the work that we’ve done, we’ve only scratched the surface, and that surface is probably deceiving. Some classic major concepts, such as “competitive exclusion,” are so simplistic that they don’t even begin to describe nature.
The one thing that students seem to learn in school about evolution is that Lamarck was wrong, and this lesson comes with a certain example involving a giraffe. It’s taken us a couple centuries to figure out that, to a certain extent, Lamarck was quite right about the inheritance of acquired characteristics after all. He just didn’t know the mechanism was epigenetic, just as Darwin wasn’t aware of the particulate inheritance mechanisms described by Mendel. Jerry Coyne addressed this a score of moons ago.
In short, some things we think we fundamentally understand, we really don’t. This is particularly the case for complex phenomena that are explained by theories requiring mechanisms that can’t be readily measured in nature. Natural selection is very straightforward and observable, and we have that one locked down. But many more intricate concepts in ecology? I wouldn’t buy stock in them.
If your research program is oriented towards testing theories, then you’re less likely to stumble on a new perspective.
When I design experiments, I “tinker” with natural systems by tweaking them in small ways to see what happens. I do this because I find something that’s curious to me, and I want to understand what’s happening in that system. I don’t pretend that what I find will answer a grand theory or unify different branches of our disciplines. I just want to get a little answer about a little thing that’s curious. My suspicion, that might approach something resembling belief, is that this kind of work will help us learn more about the world than most theoretically-driven research. I think that most of our major advances came from this kind of approach as well.
You’lll find some mildly unflattering things said about this approach, over at Dynamic Ecology. This is a healthful disagreement of opinion. (Heck, there might even be a claim that it wasn’t unflattering!) I recognize that what I’m writing goes against current dogma, that if your work isn’t driven by theory, then it’s not of much value. I can respectfully disagree, but then again, there’s no major concept or principle with my name on it, either, so I can’t push my point too firmly.
If you take a walk through a rainforest, a few hundred curiosities, with no known answers, should slap you in the face very quickly. This happens during a walk during the desert, as well, though with lower frequency as there’s less biomass.
When I walk through the rainforest, I see something new every time I step out. Among the things that visibly move under their own power, ants are clearly the dominant feature of rainforests. If I want to be able to ask a whole bunch of questions, and had to pick a taxon, ants are a good way to go. (A well known and true event is that Bert Hölldobler and Ed Wilson spent two weeks together at what is now my field site; it resulted in three very cool publications based on what they found.) One major unexplored frontier is the leaf litter of tropical rainforests. Nearly all of the the primary production of the forest ends up on this thin layer between the sky and the earth, as Jack Longino once said, and we know so little about it and its denizens. It’s a big linkage in food webs that is a huge black box with respect to most fields of ecology (aside from ecosystem ecology, though this is still not as well known as it could be in this respect).
Now you can see why I have trouble assembling an elevator talk.
I propose a taxonomy of research goals, with three domains:
- Discovery. Finding or creating something brand new – a species, a theory, a mechanism.
- Improving ideas. This is the theoretical bandwagon – amassing evidence to flesh out, support, refute or modify existing theories.
- Tinkering. There’s a little something that doesn’t make sense and you want to figure it out. Your goal is not to create a new theory or to test specific hypotheses.
Obviously the third category wouldn’t sit well with funding agencies. That’s not keeping me from adopting this approach as my primary orientation. From reading my papers, you wouldn’t necessarily be able to tell which primary goal led to a particular manuscript, though it’s almost always the result of tinkering. You can’t sell tinkering to well-read journals in the current environment. They want you start your story as if your experiment was always designed to test one very specific hypothesis, even if everybody knows that isn’t true.
When I’m wondering what project I want to do next, I do a few things. I weigh a bunch of factors – what’s fundable, what’s do-able, and what’s publishable.
Then I notice the file on my desktop, and I toss all of that crap aside.
I do that little thing that’s always been nagging: “Answer me!” Then, I go off and do that project. My only problem is that the list of nagging questions is far too long for me to answer in one lifetime.
You might be asking, “How’s that working out for ya?” I’ll get to that next week with some specific examples.
Small labs should avoid theoretical bandwagons. It’ll make it hard to get money, publish and do good work effectively.
In an earlier post, I described two categories of research: the development of new ideas, and the testing, shaping and fine-tuning of these ideas.
I said I didn’t like either of the categories. I’ll explain that next week, but to get to that point I need to explain how big labs are designed for bandwagons, and how labs at teaching institutions should avoid designing their work to address bandwagon theories.
A bandwagon — as I use it here — is any theory, topic, or issue that lots of people are working on simultaneously. What do I think are some bandwagons at the moment? It’s easy, just pop open a journal and look at the table of contents! In ecology and social insects, my two main fields, here are a few that are at some point in the bandwagon boom-and-bust cycle: functional traits to understand community structure and assembly; genomic approaches to understanding the social regulation of development; models of geographic range shifts in response to climate change; physiological and genomic mechanisms of task allocation. (You could also throw in arguing about group selection, but that’s more about yelling than data.)
I’m not saying that the scientific community doesn’t need this work to happen. All of these topics are very interesting, and people have chosen them because they’re ripe for discovery and progress. It’s not a bad thing that these topics are bandwagons. When great ideas come along, we need people to work on them, including both disagreements and points of consensus. This is the standard practice of science.
It’s so much the standard practice of science, that labs at research institutions are engineered to thrive while working on bandwagons. Race cars are built for speed, thermoses are designed to keep your drinks hot, and many big research labs are designed to produce bandwagon research. (Not all big labs do, but they can be easily engineered to do so if this is the goal of the PI.)
If you’re running your own small lab at a teaching institution, there are a number of major strategic disadvantages from working on the same questions as big labs. These are disadvantages because they make it harder for the lab to get grants, publish papers, have a visible research profile, develop collaborations and provide the best opportunities for students.
No matter what you do, you won’t be perceived as the primary expert on the bandwagon topic. There will always be someone who is considered to be the authority, who is more productive on the topic. This person will have a whole lab working alongside them on the same topic. Moreover, this person’s name tag at conferences will have the name of big of a research university next to their own. Does this perception as an expert matter? Sure it does. This kind of perception enables you to do better science and gives better resources for your students.
Big labs can mobilize to jump on bandwagons quickly. They can turn on a dime by having a new dissertation start on the project, or assigning a postdoc to it. (You’re thinking, dissertations don’t start overnight?! Compared to the timescale of when I start and finish projects, they do. Tomorrow is a story about a quick project done in 2008 but was published this year. That’s par on my course. The manuscript I’m editing today has has had all of the data assembled on my hard drive for seven years. And I’ve been thrilled about it the whole time, too. And – get this – it’s still not stale. It’s actually ripened.)
You don’t want to work on a specific aspect of a project when other bigger labs will get to them quickly. Moreover, big labs will work so quickly that they will exhaust it before you get finished. In ecology, for example, thank goodness I didn’t work on the mid-domain effect myself or I would have entirely missed that wave before I even submitted my first paper. I would like to work on functional traits in ants, as the ideas seem interesting, but the same thing will happen to me if I do that. My paper would be passé by the time I tried to publish it.
Big labs need big funding. Theoretical bandwagons are the things that attract dollars. They can be sold as “transformational” research that NSF is seeking to support. Most of these potentially transformative projects will end up in the dustbin of history, and a small fraction will result in big change. If you’re a big lab and you need to pay for people, then you better hop on board! If you don’t, you’ll have trouble keeping staffed. If you’re top notch, you an create your own bandwagon. But if you catch it in the first couple years, then you can still get in there for one grant cycle, or maybe even two. Following the same principle, bandwagons are horrible for small labs because they can never compete with these big labs that are putting in proposals on the same question. They’d never survive a side-by-side comparison once you put the biosketches up against one another. Of course they’ll fund the lab that they think will get 10-20 papers out of a project when they think you’ll only get a few out of it. So stay away unless you have the record to show that you can beat the top labs riding the same bandwagon.
To be clear: I am not suggesting that scientists at teaching schools specialize on an obscure topic that nobody is interested in, that can be mined for a series of novel but inconsequential publications.
I not suggesting that you stay fully clear of theoretical bandwagons under all circumstances, but only that if you hop on it should be with a big lab that is ready to roll. You also could take an existing project of yours and sell it this way, if you wish, though that will shorten its shelf life.
Next week, I’ll share a taxonomy of research goals, which will explain how I think you can do novel and truly meaningful research without chasing theories-of-the moment.
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.
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.