I blog a lot about how individual scientists, and whole fields, choose and change their direction. When do they change their minds, get caught up in controversies, jump on bandwagons, fall prey to zombie ideas?
So here’s a question for you: have you ever abandoned a big line of research? Or, if you don’t feel like you’ve ever abandoned anything, what’s the biggest change of direction you’ve ever made in your work? Or the biggest line of research you’ve ever set aside or put on the back burner? And why?
I ask about a “big” line of research because everybody tweaks the details of their methods and approaches all the time. I’m not asking about whether you changed from one programming language to another, or whether you once abandoned one statistical analysis in favor of an alternative analysis, or etc. I’m asking about things like a big question that you used to work on but don’t anymore, or a system you once worked in but stopped, or a big project that you abandoned mid-stream, or completed but never followed up even though you’d originally planned to follow it up. I’m asking about giving up on something or setting it aside, even though you were pretty heavily invested in it. So that you may not have wanted to give it up or set it aside, might even have had strong reasons to stick with it. For any Lakatos fans out there (hi Brian!), I’m basically asking whether you’ve ever given up on or radically changed your own “research program”, or an important part of it.
So I’m not thinking of cases where you finished a line of research to your own satisfaction, and so then started something else. Like when you finish reading a book and start a new one. I’m thinking of cases analogous to not finishing the book you’re reading. Nor am I thinking of cases where you start up a new line of research, but continue to pursue the old one but devote less time to it. That’s like starting a second book while continuing to read the first.
I’m most interested in cases of people abandoning or moving away from a line of research that was well-developed and ongoing. As opposed to people tentatively exploring a line of research and deciding early on not to pursue it. But feel free to chime in with stories about both more- and less well-developed lines of research. If the best answer you have is like starting a book but then abandoning it ten pages in, that’s ok. 🙂
I can imagine many possible reasons for giving up on or setting aside a big line of research. One important but somewhat mundane set of reasons has to do with external events. The person leading the work left your group, causing you to abandon that line of work. The work ran into insurmountable technical obstacles. There was a natural disaster or a war in your study area. You ran out of grant money and couldn’t get more. You discovered that someone else had already done or was doing the same thing. You weren’t able to convince enough people to share their data with you. Etc. In all these cases, you wanted to keep pursuing the research, but you couldn’t.
A more interesting case is triage: you had too much on your plate, so you had to put something on the back burner. Which leads to the question, how did you decide what line of research to leave “in the waiting room” and which one to “admit”? Meg’s talked about this before.
The most interesting case, at least to me, is when someone chooses to set aside or abandon a line of research they could’ve kept pursuing had they wanted to, and not at the expense of some other line of research. I suspect this kind of thing is fairly rare, which is part of why I find it interesting. Have you ever decided that a big question you once thought was interesting and important actually wasn’t? At least not relative to some other, completely different question that you decided to pursue instead? Have you ever changed from one study system to a completely different one? (That’s common during grad school, and during the grad school-to-postdoc transition, but surely less common afterwards) Did you decide that the fundamental research you’d been doing just wasn’t making enough concrete, immediate difference in the world, so decided to do applied work instead? (I bet that one might be fairly common, actually) Did you ever read a blog post or watch a debate and suddenly decide, “Hey, I’m working on a zombie idea, I ought to work on something else!”* 🙂
I can imagine intermediate cases between choosing to abandon a line of research and being forced to do so. For instance, you could keep pursing the work, but it would be a pain because funding is increasingly difficult to get or it’s getting harder to get the permits or something. So you decide to do something else that’s easier to do.
I can think of some pretty well-known examples of ecologists and evolutionary biologists changing direction in big ways, though I don’t always know the reasons. Indeed, with one exception I don’t even know if these were cases of the sort I’m asking about, as opposed to cases of people changing direction after having completed a previous line of research to their own satisfaction. Nor do I know if changes of direction that seem big to me seem equally big to the people who made them. Peter Morin switched from working on amphibians to working in protist microcosms because he wanted to ask questions about long-term community dynamics. Dave Tilman switched from working on algae in chemostats to working on grassland plants, although he continued to ask the same sorts of big questions about resource competition. Joan Roughgarden famously turned her attention from population biology to the evolution of sexual behavior. I’m sure there are other examples I’m not thinking of off the top of my head.
I’ve never totally abandoned or set aside a big line of research myself. The closest I’ve ever come was a period when I actively avoided trying to dream up possible applications of the Price equation. I’d written several papers on that already, and I got worried that I was treating the Price equation as a hammer in search of a nail. Thereby running the risk of trying to “hammer” on things that shouldn’t be hammered on. But I’ve since been drawn back into it because colleagues approached me asking for my help in applying the Price equation to their own projects. So you could perhaps say that I abandoned that line of research, depending on whether you think of me as still pursuing it by participating in collaborations initiated by others. On the other hand, at this point I’m pretty satisfied with my body of work on the Price equation, it doesn’t feel incomplete to me. Although I might return to it if a good idea happens to strike me.
Looking forward to your comments.
*I’ll wager a beer that nobody ever has abandoned a line of research for that last reason. Anyone want to take the other side of that bet? 🙂
I did. Spent about three years before and during grad school, studying plant molecular genetics and evolution, including class and lab work, grad school applications etc.; went all in. Finally realized I just did not want to spend those huge numbers of hours in a laboratory, no matter how intellectually fascinating and important it was (and it was), and just dropped it. Now I have a much better understanding of statistics and could conceivably get back into the field through quantitative “omics” analyses, which is amazing and highly important stuff, though it’s unlikely I ever will.
In ecology, I worked for several years on the topic of estimating American pre-settlement forest conditions, including my dissertation and a few publications, and then dropped it over the last few, but am returning to it. Discouragingly few are interested in the historical context, and funding amounts are small and far between, though I did get some. Mainly it’s just interesting to me.
Pre-dispersal seed predation was a big part of my PhD as I was looking at biotic factors which could lead to selection on flowering time in a perennial herb. The data from this were included within the main paper that came out of the thesis and a smaller note about how even small seeds can survive partial pre-dispersal seed predation, including loss of around 50% of seed mass. I’ve not worked on it since, which is a shame because I think it’s a fascinating area of study, but there’s just not time to do everything!
Like Jeff, I drifted away from studying pre-dispersal seed predation, even though I still think it is really interesting with lots of important questions. They were supposed to play a big role in my PhD project but although I had lots of seed herbivory, I was never able to shed any light on it. Seems like they cared about all the traits I wasn’t measuring. So I continue to account for them, but only to say that they don’t matter for what I’m studying… And other projects (in different systems) that feature seed predators haven’t been funded. Someday I’ll probably get back to studying them though, so I’m not sure we can classify it as a permanent abandonment. Good to know that I’m in good company though!
We should form a club 🙂
I spent a few years trying to develop a rotifer-parasite system. It was promising enough that I still sometimes wonder if I should try again. But, in the end, I just couldn’t get the system working reliably enough in the lab to feel like I could really run with it, so I decided to cut off our work on it. It’s more along the lines of stopping a book after the first chapter, but it was a long first chapter with some really interesting themes, so I still feel like I had invested a lot in it!