Embracing failure: How research projects are like startups
As an academic who’s spent time in the startup world, I see strong similarities between the nature of a scientific research project and the nature of a startup. This boils down the fact that most research projects fail (in a sense that I’ll describe), and even among the successful projects the variance is extremely high — most of the impact is concentrated in a few big winners.
Of course, research projects are clearly unlike startups in some important ways: in research you don’t get to capture the economic benefit of your work; your personal gain from success is not money but academic reputation (unless you commercialize your research and start an actual startup, but that’s not what this post is about at all.) The potential personal downside is also lower for various reasons. But while the differences are obvious, the similarities call for some analysis.
I hope this post is useful to grad students in particular in acquiring a long-term vision for how to approach their research and how to maximize the odds of success. But perhaps others including non-researchers will also find something useful here. There are many aspects of research that may appear confusing or pathological, and at least some of them can be better understood by focusing on the high variance in research impact.
1. Most research projects fail.
To me, publication alone does not constitute success; rather, the goal of a research project is to impact the world, either directly or by influencing future research. Under this definition, the vast majority of research ideas, even if published, are forgotten in a few years. Citation counts estimate impact more accurately , but I think they still significantly underestimate the skew.
The fact that most research projects don’t make a meaningful lasting impact is OK — just as the fact that most startups fail is not an indictment of entrepreneurship.
A researcher might choose to take a self-interested view and not care about impact, but even in this view, merely aiming to get papers published is not a good long-term strategy. For example, during my recent interview tour, I got a glimpse into how candidates are evaluated, and I don’t think someone with a slew of meaningless publications would have gotten very far. 
2. Grad students: diversify your portfolio!
Given that failure is likely (and for reasons you can’t necessarily control), spending your whole Ph.D. trying to crack one hard problem is a highly risky strategy. Instead, you should work on multiple projects during your Ph.D., at least at the beginning. This can be either sequential or parallel; the former is more similar to the startup paradigm (“fail-fast”).
I achieved diversity by accident. Halfway through my Ph.D. there were at least half a dozen disparate research topics where I’d made some headway (some publications, some works in progress, some promising ideas). Although I felt I was directionless, this turned out to be the right approach in retrospect. I caught a lucky break on one of them — anonymity in sanitized databases — because of the Netflix Prize dataset, and from then on I doubled down to focus on deanonymization. This breadth-then-depth approach paid off.
3. Go for the big hits.
Paul Graham’s fascinating essay Black Swan Farming is about how skewed the returns are in early-stage startup investing. Just two of the several hundred companies that YCombinator has funded are responsible for 75% of the returns, and in each batch one company outshines all the rest.
The returns from research aren’t quite as skewed, but they’re skewed enough to be highly counterintuitive. This means researchers must explicitly account for the skew in selecting problems to work on. Following one’s intuition and/or the crowd is likely to lead to a mediocre career filled with incremental, marginally publishable results. The goal is to do something that’s not just new and interesting, but which people will remember in ten years, and the latter can’t necessarily be predicted based on the amount of buzz a problem is generating in the community right now. Breakthroughs often come from unsexy problems (more on that below).
There’s a bit of a tension between going for the hits and diversifying your portfolio. If you work on too few projects, you incur the risk that none of them will pan out. If you work on too many, you spread yourself too thin, the quality of each one suffers, and lowers the chance that at least one of them will be a big hit. Everyone must find their own sweet spot. One piece of advice given to junior professors is to “learn to say no.”
4. Find good ideas that look like bad ideas.
How do you predict if an idea you have is likely to lead to success, especially a big one? Again let’s turn to Paul Graham in Black Swan Farming:
“the best startup ideas seem at first like bad ideas. … if a good idea were obviously good, someone else would already have done it. So the most successful founders tend to work on ideas that few beside them realize are good.”
Something very similar is true in research. There are some problems that everyone realizes are important. If you want to solve such a problem, you have to be smarter than most others working on it and be at least a little bit lucky. Craig Gentry, for example, invented Fully Homomorphic Encryption mostly by being very, very smart.
Then there are research problems that are analogous to Graham’s good ideas that initially look bad. These fall into two categories: 1. research problems that no one has realized are important 2. problems that everyone considers prohibitively difficult but which turn out to have a back door.
If you feel you are in a position to take on obviously important problems, more power to you. I try to work on problems that everyone seems to think are bad ideas (either unimportant or too difficult), but where I have some “unfair advantage” that leads me to think otherwise. Of course, a lot of the time they are right, but sometimes they are not. Let me give two examples.
I consider Adnostic (online behavioral advertising without tracking) to be moderately successful: it has had an impact on other research in the area, as well as in policy circles as an existence proof of behavioral-advertising-with-privacy. Now, my coauthors started working on it before I joined them, so I can take none of the credit for problem selection. But it’s a good illustration of the principle. The main reason they decided this problem was important was that privacy advocates were up in arms about online tracking. Almost no one in the computer science community was studying the topic, because they felt that simply blocking trackers was an adequate solution. So this was a case of picking a problem that people didn’t realize was important. Three years later it’s become a very crowded research space.
Another example is my work with Shmatikov on deanonymizing social networks by being able to find a matching between the nodes of two social graphs. Most people I talked to at the time thought this was impossible — after all, it’s a much harder version of graph isomorphism, and we’re talking about graphs with millions of nodes. Here’s the catch: people intuitively think graph isomorphism is “hard,” but it is in fact not NP-complete and on real-world graphs it embarrassingly easy. We knew this, and even though the social network matching problem is harder than graph isomorphism, we thought it was still doable. In the end it took months of work, but fortunately it was just within the realm of possibility.
5. Most researchers are known for only one or two things.
Let me end with an interesting side effect of the high-skew theory: a successful researcher may have worked on many successful projects during their career, but the top one or two of those will likely be far better known than the rest. This seems to be borne out empirically, and a source of much annoyance for many researchers to be pigeonholed as “the person who did X.” Let’s take Ron Rivest who’s been prolific for several decades not just in cryptography but also in algorithms and lately in voting. Most computer scientists will recall that he’s the R in RSA, but knowledge of his work drops off sharply after that. This is also reflected in the citation counts (the first entry is a textbook, not a research paper). 
In summary, if you’re a researcher, think carefully about which projects to work on and what the individual and overall chances of success are. And if you’re someone who’s skeptical about academia because your friend who dropped out of a Ph.D. after their project failed convinced you that all research is useless, I hope this post got you to think twice.
I may do a follow-up post examining whether ideas are as valuable as they are held to be in the research community, or whether research ideas are more similar to startup ideas in that it’s really execution and selling that lead to success.
 For example, a quarter of my papers are responsible for over 80% of my citations.
 That said, I will get a much better idea in the next few months from the other side of the table :)
 Specifically, it undermines the “we can’t stop tracking because it would kill our business model” argument that companies love to make when faced with pressure from privacy advocates and regulators.
 To be clear, my point is that Rivest’s citation counts drop off relative to his most well-known works.
Thanks to Joe Bonneau for comments on a draft.