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Why I don't like the PhD system


Fermi's rejection of our work
Freeman Dyson Scientist
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So I was in a high state of enthusiasm and I decided I would go to Chicago and show these results to Fermi and tell him how well we were doing. We wanted to have Fermi's blessing on our efforts as he was really the prime mover in this whole subject, and it was a good opportunity for me to get to know Fermi. Anyway, I arranged through Hans Bethe to go to Chicago and tell him about what we were doing. So I arrived at Chicago and knocked on Fermi's door, and he was very polite. I came in, and he said, 'Yes?' and I showed him the graphs on which our experiment, our theoretical numbers were plotted and Fermi's experimental numbers were plotted, and the agreement was on the whole pretty good. And Fermi hardly looked at these graphs, he just put them on the desk, just glanced at them very briefly and he said, 'I am not very impressed with what you've been doing.' And he said, 'When one does a theoretical calculation, you know, there are two ways of doing it. Either you should have a clear physical model in mind, or you should have a rigorous mathematical basis. You have neither.' So that was it - in about two sentences he disposed of the whole subject. Well then I asked him, well what does he think about the numerical agreement, and he said, 'How many parameters did you use for the fitting? How many free parameters are there in your method?' So I counted up. It turned out there were four. And he said, 'You know, Johnny von Neumann always used to say, "With four parameters I can fit an elephant, and with five I can make him wiggle his trunk." So I don't find the numerical agreement very impressive either.' So I said, 'Thank you very much for you help,' and I said goodbye. There was nothing more to be said. The whole discussion took maybe 10 or 15 minutes. And I came back to Cornell to tell the team the bad news. So that was another watershed in my life, and I think it was profoundly useful what Fermi did. He had this amazing intuition. He could spot what was good and what was bad right away. I mean, we might have worked on these calculations for five years if Fermi hadn't given us the red light and, as it was, Fermi was absolutely right because in the end of course it turned out that the theory on which we based the whole calculation was an illusion. There is really no such thing as a pseudo-scalar theory of pions. In reality 10 years later, or whenever it was, quarks were invented and the whole theory of the strong interactions was totally transformed into a theory of quarks, and it's only when you represent the pion as a compound system of two quarks that you can begin to have a real physical theory. So our whole physical basis was wrong, and so it was perfectly true that any experimental agreement we found was illusory, but it took Fermi to see that and he could see it without knowing about quarks - of course nobody had dreamed of quarks at that time - but he felt in his bones that this theory was no good. And he was right. So he saved us maybe five years of blind work and so I'm extremely grateful to him for that. But it was a tough situation for us, especially because we had some graduate students involved in this project. They depended on it for their PhD thesis, so it was difficult. I mean I simply had to tell the team, 'Look, I'm sorry, but this is not going anywhere, so all we can do is write up what we've done and publish it but it's not going to go any further, and you'd better find some other line of work.' So it was not a very pleasant experience for the graduate students or for me. But in the end, of course, it was for the good of us all. But that's the kind of genius that Fermi had, and I think that showed me very clearly that I wasn't a particle physicist, that I didn't have that kind of instinct. I mean, that my gifts are in mathematics and not basically in physics. So when there's a theory that is well based on physics, as it was in the case of quantum electrodynamics, then I can do marvellously well with using it, but I'm not able to invent a new theory, and what was required for the strong interactions was an invention, and that clearly wasn't my cup of tea. And so from that time on I didn't seriously try to solve the problem of strong interactions. From that time on I worked in field theory on the mathematical side, which I could do very happily and even usefully, so from that time on I was interested in the mathematics of field theory and I got involved in the Whiteman programme of trying to establish quantum field theory axiomatically, and deducing from axioms physical consequences. That's something that I love to do which is, in Fermi's terminology, based on a firm mathematical basis; whether it's physically correct or not, it's certainly mathematically sound. So I made that choice that I would go with the mathematics and not with the physics.

Born in England in 1923, Freeman Dyson moved to Cornell University after graduating from Cambridge University with a BA in Mathematics. He subsequently became a professor and worked on nuclear reactors, solid state physics, ferromagnetism, astrophysics and biology. He has published several books and, among other honours, has been awarded the Heineman Prize and the Royal Society's Hughes Medal.

Listeners: Sam Schweber

Silvan Sam Schweber is the Koret Professor of the History of Ideas and Professor of Physics at Brandeis University, and a Faculty Associate in the Department of the History of Science at Harvard University. He is the author of a history of the development of quantum electro mechanics, "QED and the men who made it", and has recently completed a biography of Hans Bethe and the history of nuclear weapons development, "In the Shadow of the Bomb: Oppenheimer, Bethe, and the Moral Responsibility of the Scientist" (Princeton University Press, 2000).

Tags: Chicago University, Enrico Fermi, Hans Bethe, John von Neumann

Duration: 6 minutes, 36 seconds

Date story recorded: June 1998

Date story went live: 24 January 2008