Doing less risky research is more risky for your career
December 2014 (perspective of an assistant professor)
I'm writing this article on my iPhone at a coffee shop.
Start time: 5:23pm
Doing less risky work is more risky for your career
In this article I want to explore the idea that attempting to do supposedly less risky work is actually MORE risky for one's career.
What I say probably applies most to design and technology careers like the one I'm currently in as a computer science researcher. In contrast, I wouldn't want my doctor or car mechanic trying out random funky shit in their jobs; for the majority of jobs, the less risky, tried-and-true approach is wiser.
As a researcher, our primary output is a peer-reviewed publication describing a novel idea and some evidence that the idea has merit. (A related "input" is a successful grant proposal, which provides much-needed funding for us to produce research that leads to publication, which leads to further grants, and so on until the cycle runs dry.)
To build a career as a well-respected researcher, we must publish papers in top-tier (and some second-tier) venues. Each respectable venue accepts 12% to 25% of all submissions. Each submission gets 3 to 5 reviews from anonymous colleagues in one's field. So the name of the game is to get good enough reviews to boost your paper submission into the top 12% to 25% so that it can get accepted for publication.
Reviewers are volunteers who are often busy and overworked, so they can usually devote less than an hour to consider each paper. (You might have spent 1,000 hours working on the research that led to this paper. But it only gets less than 1 hour of consideration from each reviewer.)
Since a reviewer has so little time, they form a gut reaction of each paper on two main dimensions:
If they answer Yes to both questions, then they will give a favorable review. If they answer No, then they will vote to reject the paper.
Assuming that you're even halfway legit, you won't submit a paper that falls into the No/No category. And if you're so good that you're always submitting Yes/Yes papers, then you probably have more productive things to do than reading this article :)
Most legit papers are Yes/No or No/Yes. That is, they're either exciting but not too well carried out. Or they're boring but well carried out.
So which is better? I strongly believe that exciting but not well carried out papers (Yes/No) are more likely to get positive reviews than boring but well carried out papers (No/Yes).
The worst review you can get is something like "meh there was nothing really wrong with this paper, everything was done well ... but the topic is just too incremental and boring." Of course polite reviewers will choose more diplomatic wording, but this is what they mean. Papers with mediocre reviews rarely make the cut.
On the other hand, if your idea is exciting but the execution is lacking a bit in rigor, then reviewers MIGHT cut you some slack since they want to see an exciting idea out in print. You might get some negative reviews for sloppiness but hopefully some enthusiastic ones as well from reviewers who empathize with your cause.
This observation has affected what projects I choose to undertake in my own research. When I was younger, I used to think that "playing it safe" by executing well on incremental projects that don't rock the boat was the best way to consistently get published. But now I realize that most of those papers will be lumped into the boring-but-well-done category, which inevitably get rejected.
If I take on more ambitious projects, that's the only way to write papers that excite reviewers. Of course people might hate my weird ideas, but at least they stand a chance of getting sympathy from certain reviewers. Whereas a boring idea, no matter how well executed, will always result in mediocre "meh" type of reviews that lead to rejection.
So in my research career, taking on higher-risk projects is, paradoxically, less risky for my career since they stand SOME chance of getting published at top-tier venues, whereas spending all of my time executing rigorously on boring, incremental, predictable, tried-and-true ideas will mostly lead to those papers getting rejected.
This realization is important because it takes roughly the same amount of time to carry through on an exciting idea as a boring idea. So picking an idea to go after is crucial, since it means that I (or my students) now don't have the time to work on another idea. So when we generate ideas now, we take that opportunity cost into account and bias toward more exciting but potentially flaky ideas.
Also, another benefit of picking an exciting idea over a boring one is that you and your collaborators are more pumped to work on it day after day, even when the going gets tough. You'll think harder about it and obsess deeper. In the end, you'll do better work than if you had gone after a supposedly safe idea that you just treat as a chore.
But it's scary to go down a path that isn't just making incremental improvements, since there's a fear that what you're attempting is TOO FAR AWAY from the tastes of the current mainstream in your field to get accepted. That's a legitimate risk, and it's an art to balance weirdness and acceptability for the sake of your career. I don't claim to know how to do that yet.
I've heard similar anecdotes from peers who are trying to build high-tech products, especially in the consumer sector. They tell me that it's better to make something that a few people LOVE and will tell their friends about (even if other people hate it) rather than inventing something boring but solid that nobody especially likes but doesn't hate either. Again, something that seems high risk is actually the lower risk choice, since the "safe" (boring) choice will most likely lead to failure.
End time: 6:09pm
(This article was written entirely on my iPhone with no edits afterward.)