A piece of wisdom I have heard several times is that an academic should change their direction of research roughly every seven years. This change needs not be radical but clearly more than what you naturally do within those seven years.

Does anybody have a reliable source for this rule of thumb? I heard this being attributed to Feynman, but neither with nor without his name can I find something on the Internet. I may have gotten the details of the quote wrong of course (e.g., seven instead of eight years).

Please mind that this is not about whether this advice is actually valid or why it may be.

  • One of the most wise methodologies for those who seek anything. Change is more cerebral than habit, to vary habitats and occupations. Commented May 28, 2023 at 12:36
  • Sounds like a good excuse to switch research to how often one should switch research directions. Commented May 28, 2023 at 20:09

4 Answers 4


I think I found it! Richard Hamming, mathematician and Turing Award recipient said it in a 1986 seminar at Bell Labs. The talk was titled "You and Your Research", and a transcript is available here. The most relevant part is in the Q&A session after the main talk:

Question: You mentioned the problem of the Nobel Prize and the subsequent notoriety of what was done to some of the careers. Isn't that kind of a much more broad problem of fame? What can one do?

Hamming: Some things you could do are the following. Somewhere around every seven years make a significant, if not complete, shift in your field. Thus, I shifted from numerical analysis, to hardware, to software, and so on, periodically, because you tend to use up your ideas. When you go to a new field, you have to start over as a baby. You are no longer the big mukity muk and you can start back there and you can start planting those acorns which will become the giant oaks. Shannon, I believe, ruined himself. In fact when he left Bell Labs, I said, "That's the end of Shannon's scientific career." I received a lot of flak from my friends who said that Shannon was just as smart as ever. I said, "Yes, he'll be just as smart, but that's the end of his scientific career," and I truly believe it was.

You have to change. You get tired after a while; you use up your originality in one field. You need to get something nearby. I'm not saying that you shift from music to theoretical physics to English literature; I mean within your field you should shift areas so that you don't go stale. You couldn't get away with forcing a change every seven years, but if you could, I would require a condition for doing research, being that you will change your field of research every seven years with a reasonable definition of what it means, or at the end of 10 years, management has the right to compel you to change. I would insist on a change because I'm serious. What happens to the old fellows is that they get a technique going; they keep on using it. They were marching in that direction which was right then, but the world changes. There's the new direction; but the old fellows are still marching in their former direction.

You need to get into a new field to get new viewpoints, and before you use up all the old ones. You can do something about this, but it takes effort and energy. It takes courage to say, "Yes, I will give up my great reputation." For example, when error correcting codes were well launched, having these theories, I said, "Hamming, you are going to quit reading papers in the field; you are going to ignore it completely; you are going to try and do something else other than coast on that." I deliberately refused to go on in that field. I wouldn't even read papers to try to force myself to have a chance to do something else. I managed myself, which is what I'm preaching in this whole talk. Knowing many of my own faults, I manage myself. I have a lot of faults, so I've got a lot of problems, i.e. a lot of possibilities of management.

The Shannon referred to in the quote would be Claude E. Shannon, who is often called "the father of information theory". Shannon laid the foundations for this discipline while at Bell Labs, and in his talk Hamming suggests that Shannon would not continue to "plant acorns" afterwards.

While it isn't really phrased as a recommendation for others, it is perhaps also worth noting that Donald Cram (1987 Nobel laureate in chemistry) has said

To retain my fascination with chemistry, I have had to change my research fields about every 10 years.

This quote can be found in I. Hargittai (2003) Candid Science III: More Conversations with Famous Chemists. Imperial College Press, p. 192.

  • 3
    Thanks for finding this, really interesting. Commented May 28, 2023 at 2:39
  • 1
    Hamming was indeed a fascinating personality. His mathematical books on numerical analysis, probability and digital filters, even though somehow outdated now, are an interesting reading nonetheless. Commented May 28, 2023 at 12:23
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    I read once that Hamming would ask interview candidates: "What's the most important problem in your field?" And then he'd follow up by asking "Why aren't you working on it?"
    – davidbak
    Commented May 28, 2023 at 17:08
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    P.S. His Book The Art Of Doing Science And Engineering - Learning To Learn is well worth reading (and there's a beautiful edition of it from Stripe Press).
    – davidbak
    Commented May 28, 2023 at 17:09

I am sure many scholars came up with this piece of advice. This is an excerpt from an interview with Ludvig Faddeev published in the newspaper of Saint Petersburg State University, № 5 (3791), 30.03.2009:

I recall, many told me: "Why are you abandoning this gold mine? You have just started it, and it's high time to develop it. Keep on digging..." I am, however, dead set against digging gold mines. And this is what I have preached to my disciples: if you have written five works on a certain topic -- leave it and seek another topic. It is important to switch topics... As a result of this, my disciples and I have a broad variety of directions of research.

However, in academic folklore this piece of advice of his was known long before that. I learned about this rule of Faddeev, through word of mouth, back in my undergraduate years in Saint Petersburg, which was in the early 1980s.

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    I was fortunate to attend a talk by Richard Bellman around 1970, and he recommended inventing a new field, finding the early and easy results, then moving on and letting others find and prove the obscure and difficult theorems. Commented May 30, 2023 at 2:21

Paul Halmos in his biography I Want to Be a Mathematician (1985) raised that point several times, however he gave himself only five years. Here are some excerpts:

I had a theory, first subconscious and later deliberate, that the way to stay young is to change fields often. I never did become an algebraist, but I did change from measure theory (under which I mean to include probability and ergodic theory) to Hilbert space, then to algebraic logic, and then back to Hilbert space, with some dabbling with topological groups and statistics sprinkled in. After about thirty years, around 1968, I realized that I wasn't likely to be able to change again, and, at about the same time, I started writing more expository papers (such as "Ten problems in Hilbert space") and sermons (such as "How to write mathematics").

In the late 1940's I began to act on one of my beliefs: to stay young, you have to change fields every five years. Looking back on it I can now see a couple of aspects of that glib commandment that weren't always obvious. One; I didn't first discover it and then act on it, but, instead, noting that I did in fact seem to change directions every so often, I made a virtue out of a fact and formulated it as a piece of wisdom. Two: it works. A creative thinker is alive only so long as he grows; you have to keep learning new things to understand the old. You don't really have to change fields—but you must stoke the furnace, branch out, make a strenuous effort to keep from being locked in.


The physicist George Uhlenbeck was another famous scientist known for repeating a maxim like this, although I don't know whether he every specified how long one should pursue an area of research before changing to something else. Uhlenbeck's student Seth Putterman described his advisor's view in the introduction to Putterman's book, Superfluid Hydrodynamics:

In April 1968 during my second year as a graduate student at the Rockefeller University I was one afternoon surprised to see upon entering my thesis adviser’s office, a large pile of books and papers dealing with superfluidity. My adviser G. E. Uhlenbeck proceeded to ask me if I knew of any other works on this subject. I replied by asking what had brought about this shift of emphasis away from relativistic thermodynamics. His answer was that changing fields was a time tested means of renewing himself and to bring it about he had committed himself to give a course on superfluidity (along with T. M. Sanders, Jr.) in the 1968 summer school at the University of Colorado. In this way he assured me that his course would also fulfill the first requirement of Ehrenfest: that the teacher learn something.

He first became famous for co-devising (with Samuel Goudsmit, when they were both graduate students of Paul Ehrenfest) the idea of electron spin, but he changed topics frequently. Over time, he worked a wide range of topics related to statistical, thermal, and fluid mechanics: the quantum Boltzmann equation, biased and damped Brownian motion, the relativistic thermodynamics that Putterman had been expecting to work on, and superfluidity.

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