Sunday, February 2, 2014

Black sheep

"Publish or Perish" has become a motto for academics, but it is hard not to get depressed about this rat race in academia. I see researchers who have published an implausible amount of papers in good venues, but they still remain obscure. With all those papers, they haven't even made a splash in their field of study. I then ask myself what chance I stand for making a big enough contribution to be useful. Then, I proceed to have my semi-annual existential crisis, and question the point of publishing and my career in academia. I recover in a couple days generally, because I like working on problems and I am curious about stuff. But, these questions loom: Am I wasting my time? Am I irrelevant with my publications? How should I allocate/manage my time to be useful?

Publish less? 

It is simplistic to say "It is the quality that counts. If you publish less you will publish better quality work and get recognition". Experience refutes this. If you strive to publish less, and hold your self to imaginary/unattainable standards, it will actually harm your impact. Feynman talks about the "Nobel Prize effect" in his memoir. Hamming describes the Nobel Prize effect as follows:

The day the prize was announced we all assembled in Arnold Auditorium; all three winners got up and made speeches. The third one, Brattain, practically with tears in his eyes, said, "I know about this Nobel-Prize effect and I am not going to let it affect me; I am going to remain good old Walter Brattain." Well I said to myself, "That is nice." But in a few weeks I saw it was affecting him. Now he could only work on great problems.
When you are famous it is hard to work on small problems. This is what did Shannon in. After information theory, what do you do for an encore? The great scientists often make this error. They fail to continue to plant the little acorns from which the mighty oak trees grow. They try to get the big thing right off. And that isn't the way things go. So that is another reason why you find that when you get early recognition it seems to sterilize you. In fact I will give you my favorite quotation of many years. The Institute for Advanced Study in Princeton, in my opinion, has ruined more good scientists than any institution has created, judged by what they did before they came and judged by what they did after. Not that they weren't good afterwards, but they were superb before they got there and were only good afterwards.

Baa baa black sheep

So publishing less is bad, and publishing more does not guarantee you make an impact. Then what is a good heuristic to adopt to be useful and to have an impact?

I suggest that the rule is to "be daring, original, and bold". We certainly need more of that in the academia. The academia moves more like a herd, there are flocks here and there mowing the grass together. And staying with the herd is a conservative strategy. That way you avoid becoming an outlier, and it is easier to publish and get funded because you don't need justify/defend your research direction; it is already accepted as a safe research direction by your community. (NSF will ask to see intellectual novelty in proposals, but the NSF panel reviewers will be unhappy if a proposal is out in left field and is attempting to break new ground. They will find a way to reject the proposal unless a panelist champions the proposal and challenges the other reviewers about their concocted reasons for rejecting. As a result, it is rare to see a proposal that suggests truly original/interesting ideas and directions.)

To break new ground, we need more mavericks that leave the herd and explore new territory in the jungle. Looking at the most influential names in my field of study, distributed systems, I see that Lamport, Dijkstra, Lynch, Liskov were all black sheep.

Of course, when you are daring and original, you will be wrong half (?) the time. But being wrong teaches you something, and this insight will help you to have a breakthrough eventually. This is the growth mindset thinking. (I am reading the book "Mindset: The New Psychology of Success", and it is awesome. I recommend it for everyone.)

Moreover, when you are onto something really good, others will not get or accept what you are doing for a while. That's the price you pay for daring to be original. You can read several accounts of amusing paper rejections Lamport received here. However, I still think it is better to be ignored temporarily than remain unoriginal permanently. If you are not original, you are not truly contributing. Being daring and original is the only way you have for making a genuine contribution and having impact.
Don't worry about people stealing an idea. If it's original, you will have to ram it down their throats.
Howard H. Aiken

The interesting thing is, to be the black sheep, you don't need to put on an act. If you have a no bullshit attitude about research and don't take fashionable research ideas/directions just by face value, you will soon become the black sheep. But, as Feynman used to say "what do you care what other people think?". Ignore everybody, work on what you think is the right thing.

PS: Coincidentally Daniel Lemire has recently discussed about the black sheep phenomena in "To be smarter, try being crazier?"

No comments:

Two-phase commit and beyond

In this post, we model and explore the two-phase commit protocol using TLA+. The two-phase commit protocol is practical and is used in man...