After many mentor lunches, doctoral consortiums and interviewing professors for this blog, I have come across a common theme: many professors actually regret a lot.
Though the “Research Heroes” series on this blog has been full of interviews of professors saying more or less “I regret nothing,” this sentiment is not shared by many in our field. Since, it is unlikely that even 2% of the people reading this post will be as successful as the Research Heroes we have previously interviewed, it may be useful for us to listen to what other professors are saying (many who are also very successful).
So why do so many professors regret how they spent their time? It comes down to one phrase: All research is valuable, but some research is more valuable. Many professors regret working on projects that had little impact theoretically or substantively, but were safe publications. Today those publications have few cites and no practitioner has ever lifted an eyebrow at the findings.
For anonymity’s sake I will not reference the specific projects professors deemed as their “unimportant projects” but the projects they mentioned shared a number of qualities. These qualities are: 1) the findings were idiosyncratic to a domain, 2) it was difficult or pointless to apply the findings in a practical way, and 3) the findings neither answered nor stimulated any interesting questions. Oddly enough, these weaknesses could have been identified before starting the project.
Literature, parents, and religion have taught us to spend our limited time on Earth wisely. And though we may apply this wisdom to how we live our lives, we are not always good at applying it to how we do research, often chasing an idea because we think “it will work” rather than thinking, “does it matter if it works.”
Maybe try this test next time you have an idea. First tell a decision researcher and see if they think is theoretically interesting and distinct. Second, go tell a friend, significant other, or parent about your idea and see if they think it is interesting. If they don’t, you may want to reconsider the idea.
:InDecision: 
Did you ask them **why** they spent time in these uninsteresting safe publications? It isn’t simple to just bin uninteresting projects if your grant money depends on them. At least from my experience, and I might be accursed with bad luck, grant reviewing boards are very conservative. Either you have a big name on your Chief Investigators list, to whom the board won’t deny anything, or your proposal must investigate something that the board knows, from literature, is a very safe bet. And as you know, a very safe bet is a very boring bet.
Good points – I’ve asked Troy to comment as he would know better 🙂
From my talks it seems it wasn’t a matter of money. Many were well-funded professors who had the luxury of working on nearly whatever they wanted to and even these professors looked back and saw projects they felt were not optimal time spent.
I do empathize with a different point though, that is that many super successful professors say shoot for the stars, but a) don’t realize how important it just to have a solid idea or multiple publications for career purposes and b) don’t think about how us graduate students don’t have the same intellectual skills or resources to pull off such a project.
In this article my goal was just to bring up the fact that many people in our field do look back on their time and wish they’d spent it more wisely in a way that lead to true impact — however you want to define ‘impact’ as.
I’m surprised that you have not said anything about incentive systems. The current system rewards people who produce large quantities of publications in short periods that bring short-term returns. Nobody gets tenure for the influence their work will have after they are dead. So short-termism and don’t-rock-the-boat research is what gets people up the ladder. I know, I have seen enough people climbing past me by just doing ‘safe’ work. It’s easy to say how you regret doing such stuff after the fact, but maybe if you hadn’t you wouldn’t be getting interviewed…
It is possible that retrospectively some professors may engage in sort of memory distortion or incorrect weighting of factors in the past. It is possible that what was valued in their time is not as valued as today (e.g. lots of pubs).
However what this blog entry attempts to do is to balance the “I have no regrets” comments I have seen made on this blog and in other places. This viewpoint is not trying to take a stance rather just reveal information. Yet, I’ll admit, I do not like the idea for publication for publication sake, and personally do avoid that as much as possible in my academic life, even if that comes at a personal “career status” cost.
A tangential thing to think about: What is interesting about our field is how diverse thoughts about “publications” are. For instance some people highly value lots of publications and some value certain journals over others (Psych Science being a big piece of contention). One thing that is very apparent is that schools have different styles and may appreciate different types of work, so trying to align your own work style with a school may be ideal.
Probably what would have been more useful is a discussion about the extent to which these professors regret working on low-impact/safe publications AND the extent to which they thought these low-impact publications were instrumental in getting them to their current high powered positions. I always get a little annoyed when senior investigators give advice like “follow your heart” without demonstrating any self awareness of the roles that (a) dumb luck or (b) risk aversion may have played in getting them to a point where they can glibly dispense advice like “you should spend more time on risky projects that change the world”. Of COURSE these well-funded professors are lamenting the time they spent on safe projects. From their current well-funded perch it makes sense to take more risks.