Posts tagged ‘science’
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.
I’ve been on several program committees in the last year and a half. As I’ve written earlier, getting a behind-the-scenes look at how things work significantly improved my perception of research and academia. This post is a more elaborate set of observations based on my experience. It is targeted both at my colleagues with the hope of starting a discussion, as well as at outsiders as a continuation of my series on explaining how the scientific community functions (that began with the post linked above) .
Benefits of doing peer review. Peer review is often considered a burden that one grudgingly accepts in order to keep the system working. But in my experience, especially for a junior researcher, the effort is well worth the time.
The most obvious advantage of being on a PC is that it forces you to read papers. Now if you’re the type that never needs external motivation to get things accomplished, this wouldn’t matter to you — you’d do literature study on a regular basis anyway. But many of us aren’t that disciplined; I’m certainly not.
There are also insights you get that you can’t reproduce by having perfect self-discipline. PC work gives you a raw, unfiltered look into the research that people have chosen to work on. This is a 6-month-or-so head start for getting on top of emerging trends compared to only reading published papers. You also get a better idea of common pitfalls to avoid.
Finally, peer review is one of the rare opportunities to read papers critically (it is harder with published work because it doesn’t have as many loopholes). This is not a natural skill for most people — our cognitive biases predispose us to confuse good rhetoric with sound logic.
Which type of meeting? I’ve been on PCs with all three types of discussions: physical meetings, phone meetings and online. I think it’s important to have a meeting, whether physical or phone. I learn a lot, and the outcome feels fairer. Besides, quite often one reviewer is able to point out something the others have missed. Chairs of online-only PCs do try to elicit some interaction between reviewers, but for hard-to-explain but easy-to-understand reasons, the bandwidth in an interactive meeting tends to be much higher.
Phone meetings are suitable for smaller conferences and workshops. In my experience, members mostly tend to go on mute and tune out except when the papers they reviewed are being discussed. I don’t necessarily see a problem with this.
In physical meetings, I’ve found that members often make comments or voice opinions on papers they haven’t really read. I don’t think this is in the best interest of fair reviewing (although I’ve heard a contrary opinion). I wonder if a strategy involving smaller breakout groups would be more effective.
The one advantage of not having a meeting is of course that it saves time. I’ve found that the time commitment for the meeting is about a third of the reviewing time (for both physical and phone meetings), which I don’t consider to be too much of a burden given the improved outcomes.
Overall, my experience from these meetings is that members act professionally for the most part without egos or emotions getting in the way. While there is inevitably some randomness in the process, I believe that the horror stories of careless reviewers — everyone has at least one to narrate — are exaggerated. One possible reason for this misunderstanding is that there is a lot that’s discussed at meetings after the reviews are written, and often this feedback doesn’t make it into the reviews.
Problem areas. Finally, here are some aspects of PCs that I think could be improved. I have deliberately omitted the most common problems (such as an untenable number of submissions and low acceptance rates) that everybody knows and talks about. Instead, these are less frequently discussed but yet (IMO) fairly important issues.
Lost reviews. Since reviewers aren’t perfect, sometimes bad papers with persistent authors manage to get published by being resubmitted to other venues until they hit a relatively sloppy panel of reviewers. The reason this works (when it does) is that past reviews of a recycled paper are “lost”. This is a shame; it wastes reviewer effort and lowers the overall quality of publications.
Community boundaries. As a reviewer I’ve started to realize how difficult it is to publish in other communities’ venues. As an example, at security conferences we often see papers by outsiders that have something useful to say, but are unfortunately inadequately familiar with the “central dogma” of crypto/security research, namely adversarial thinking.  While I can see the temptation to reject these papers with a cursory note, I think we should be patient with these people, explain how we do things and if possible offer to work with them to improve the paper.
Unfruitful directions. Sometimes research directions don’t pan out, either because the world has moved on and the underlying assumptions are no longer true, or because the technical challenges are too hard. But researchers naturally resist having to change their research area, and so there are lots of papers written on topics that stopped being relevant years ago. The reason these papers keep getting published is that they are assigned for review to other people working in the same area. I’ve seen program chairs make an effort to push back on this, but the current situation is far from optimal.
In conclusion, my opinion is that peer review in my community is a relatively well-functioning process, albeit with a lot of scope for improvement. I believe this improvement can be accomplished in an evolutionary way without having to change anything too radically.
 The crypto/security community essentially derives its identity from adversarial thinking. Incidentally, I feel that it is not always suitable for privacy, which is why I believe computer scientists who study privacy should stop viewing ourselves as a subset of the security community.
I’ve had a wonderful time at Stanford these last couple of years, but it’s time to move on. I’m currently in the middle of my job search, looking for faculty and other research positions. In the next month or two I will be interviewing at several places. It’s been an interesting journey.
My Ph.D. years in Austin were productive and blissful. When I finished and came West, I knew I enjoyed research tremendously, but there were many aspects of research culture that made me worry if I’d fit in. I hoped my postdoc would give me some clarity.
Happily, that’s exactly what happened, especially after I started being an active participant in program committees and other community activities. It’s been an enlightening and humbling experience. I’ve come to realize that in many cases, there are perfectly good reasons why frequently-criticized aspects of the culture are just the way they are. Certainly there are still facets that are far from ideal, but my overall view of the culture of scientific research and the value of research to society is dramatically more positive than it was when I graduated.
Let me illustrate. One of my major complaints when I was in grad school was that almost nobody does interdisciplinary research (which is true — the percentage of research papers that span different disciplines is tiny). Then I actually tried doing it, and came to the obvious-in-retrospect realization that collaborating with people who don’t speak your language is hard.
Make no mistake, I’m as committed to cross-disciplinary research as I ever was (I just finished writing a grant proposal with Prof’s Helen Nissenbaum and Deirdre Mulligan). I’ve gradually been getting better at it and I expect to do a lot of it in my career. But if a researcher makes a decision to stick to their sub-discipline, I can’t really fault them for that.
As another example, consider the lack of a “publish-then-filter” model for research papers, a whole two decades after the Web made it technologically straightforward. Many people find this incomprehensibly backward and inefficient. Academia.edu founder Richard Price wrote an article two days ago arguing that the future of peer review will look like a mix of Pagerank and Twitter. Three years ago, that could have been me talking. Today my view is very different.
Science is not a popularity contest; Pagerank is irrelevant as a peer-review mechanism. Basically, scientific peer review is the only process that exists for systematically separating truths from untruths. Like democracy, it has its problems, but at least it works. Social media is probably the worst analogy — it seems to be better at amplifying falsehoods than facts. Wikipedia-style crowdsourcing has its strengths, but it can hit-or-miss.
To be clear, I think peer review is probably going to change; I would like it to be done in public, for one. But even this simple change is fraught with difficulty — how would you ensure that reviewers aren’t influenced by each others’ reviews? This is an important factor in the current system. During my program committee meetings, I came to realize just how many of these little procedures for minimizing bias are built into the system and how seriously people take the spirit of this process. Revamping peer review while keeping what works is going to be slow and challenging.
Moving on, some of my other concerns have been disappearing due to recent events. Restrictive publisher copyrights are a perfect example. I have more of a problem with this than most researchers do — I did my Master’s in India, which means I’ve been on the other side of the paywall. But it looks like that pot may finally have boiled over. I think it’s only a matter of time now before open access becomes the norm in all disciplines.
There are certainly areas where the status quo is not great and not getting any better. Today if a researcher makes a discovery that’s not significant enough to write a paper about, they choose not to share that discovery at all. Unfortunately, this is the rational behavior for a self-interested researcher, because there is no way to get credit for anything other than published papers. Michael Neilsen’s excellent book exploring the future of networked science gives me some hope that change may be on the horizon.
I hope this post has given you a more nuanced appreciation of the nature of scientific research. Misconceptions about research and especially about academia seem to be widespread among the people I talk to both online and offline; I harbored a few myself during my Ph.D., as I said earlier. So I’m thinking of doing posts like this one on a semi-regular basis on this blog or on Google+. But that will probably have to wait until after my job search is done.
Let’s take a break from the Ubercookies series. I’m at the IPAM data privacy workshop in LA, and I want to tell you about the kind of unusual scientific endeavor that it represents. I’ve recently started to write about the process of doing science, what’s good and what’s bad about it, and I expect to have more to say on this topic in this blog.
While “paradigm shift” has become a buzzword, the original sense in which Kuhn used it refers to a specific scientific process. I’ve had the rare experience of witnessing such a paradigm shift unfold, and I may even have played a small part. I am going to tell that story. I hope it will give you a “behind-the-scenes” look into how science works.
I will sidestep the question of whether data privacy is a science. I think it is a science to the extent that computer science is a science. At any rate, I think this narrative provides a nice illustration of Kuhn’s ideas.
First I need to spend some time setting up the scene and the actors. (I’m going to take some liberties and simplify things for the benefit of the broader audience, and I hope my colleagues will forgive me for it.)
The scene. Privacy research is incredibly multidisciplinary, and this workshop represents one extreme of the spectrum: the math behind data privacy. The mathematical study of privacy in databases centers on one question:
If you have a bunch of data collected from individuals, and you want to let other people do something useful with the data, such as learning correlations, how do you do it without revealing individual information?
There are roughly 3 groups that investigate this question and are represented here:
- computer scientists with a background in cryptography / theoretical CS
- computer scientists with a background in databases and data mining
This classification is neither exhaustive nor strict, but it will suffice for my current purposes.
One of the problems with science and math research is that different communities studying different aspects of the the the same problem (or even studying the same problem from different perspectives) don’t meet together very often. For one, there is a good deal of friction in overcoming the language barriers (different names/ways of thinking about the same things). For another, academics are rewarded primarily for publishing in their own communities. That is why the organizers deserve a ton of credit for bridging the barriers and getting people together.
The paradigms. There is a fundamental, inescapable tension between the utility of data and the privacy of the participants. That’s the one thing that theorists and practitioners can agree on :-) Given that fact, there are two approaches to go about building a theory of privacy-protection, which I will call utility-first and privacy-first. Statisticians and database people tend to prefer the former paradigm, and cryptographers the latter; but this is not a clean division.
Utility-first hopes to be able to preserve the statistical computations that we would want to do if we didn’t have to worry about privacy, and then ask, “how can we improve the privacy of participants while still doing all these things?” Data anonymization is one natural technique that comes out of this world view: if you are only doing simple syntactic transformations to the data, the utility of the data is not affected very much.
On the other hand, privacy-first says, “let’s first figure out a rigorously provable way to assure the privacy of participants, and then go about figuring out what are the types of computations that can be carried out under this rubric.” The community has collectively decided, with good reason, that differential privacy is the right rubric to use. To explain it properly would require many Greek symbols, so I won’t.
Privacy-first and utility-first are scientific paradigms, not theories. Neither is falsifiable. We can say that one is better, but that is a judgement.
An important caveat must be noted here. The terms do not refer to the social values of putting the utility of the data before the privacy of the participants, or vice versa. Those values are external to the model and are constraints enforced by reality. Instead, we are merely talking about which paradigm gives us better analytical techniques to achieve both the utility and privacy requirements to the extent possible.
The shift. With utility-first, you have strong, well-understood guarantees on the usefulness of the data, but typically only a heuristic analysis of privacy. What this translates to is an upper bound on privacy. With privacy-first, you have strong, well-understood privacy guarantees, but you only know how to perform certain types of computations on the data. So you have a lower bound on utility.
That’s where things get interesting. Utility-first starts to look worse as time goes on, as we discover more and more inferential techniques for breaching the privacy of participants. Privacy-first starts to look better with time, as we discover that more and more types of data-mining can be carried out due to innovative algorithms. And that is exactly how things have played out over the last few years.
I was at a similarly themed workshop at Bertinoro, Italy back in 2005, with much the same audience in attendance. Back then, the two views were about equally prevalent; the first papers on differential privacy were being written or had just been written (of course, the paradigm itself was not new). Fast forward 5 years, and the proponents of one view have started to win over the other, although we quibble to no small extent over the details. Overall, though, the shift has happened in a swift and amicable way, with both sides now largely agreeing on differential privacy.
Why did privacy-first win? I can see many reasons. The privacy protections of the utility-first techniques kept getting broken (a Kuhnian “crisis”?); the de-anonymization research that I and others worked on played a big part here. Another reason might be the way the cryptographic community operates: once they decide that a paradigm is worth investigating, they tend to jump in on it all at once and pick the bones clean. That ensured that within a few years, a huge number of results of the form “how to compute X with differential privacy” were published. A third reason might very well be the fact that these interdisciplinary workshops exist, giving us an opportunity to change each other’s minds.
The fallout. While the debate in theoretical circles seems largely over, the ripple effects are going to be felt “downstream” for a long time to come. Differential privacy is only slowly penetrating other areas of research where privacy is a peripheral but not a fundamental object of study. As for law and policy, Ohm’s paper on the failure of anonymization has certainly created a bang there.
That leaves the most important contingent: practitioners. Technology companies have been quick to learn the lessons — differential privacy was invented by Microsoft researchers — and have been studying questions like sharing search logs with differential privacy assurances and building programming systems incorporating differential privacy (see PINQ developed at Microsoft Research and Airavat funded by Google.)
Other sectors, especially medical informatics, have been far slower to adapt, and it is not clear if they ever will. Multiple speakers at this workshop dealing with applications in different sectors talked about their efforts at anonymizing high-dimensional data (good luck with that). The problems are compounded by the fact that differential privacy isn’t yet at a point where it is easily usable in applications and in many cases the upshot of the theory has been to prove that the simultaneous utility and privacy requirements simply cannot be met. It will probably be the better part of a decade before differential privacy starts to make any real headway into real-world usage.
Summary. I hope I’ve shown you what scientific “paradigms” are, how they are adopted and discarded. Paradigm shifts are important turning points for scientific disciplines and often have big consequences for society as a whole. Finally, science is not a cold sequence of deductions but is done by real people with real motivations; the scientific process has a significant social and cultural component, even if the output of science is objective.