In this ‘Short’ I’ll share a few excerpts from Feynman’s oral history that give readers an idea of:
How different journals and journal reviews were in the early/mid-1900s
The level of open-mindedness and amicable debate that characterized the physics profession at the time
And why Feynman felt the once extremely productive conferences were growing less useful later in his career
How scientists in this period utilized journals and approached conferences was remarkably productive and should serve as a source of inspiration for any readers looking to revamp how publishing and conferences work today.
Enjoy:)
Publishing in the early-20th century
Early on in this Substack, in When do ideas get easier to find?, I briefly alluded to the blistering pace of early/mid-20th century physics and how flexible researchers could be in citing something as scientific evidence. I wrote:
In 1962, Holton cited work by M.M. Kessler which found that 50% of the references cited in research papers published in the Physical Review, the top physics journal at the time, were less than three years old. And only 20% were more than seven years old. Decades on from the paradigm-changing discoveries of relativity and quantum mechanics, physics researchers had still been rapidly creating new branches of research and leapfrogging each other in the race for human progress, constantly citing younger and younger papers and letters. Science was moving so fast that a non-negligible number of citations in the journals were citing personal correspondence and conversations with other physicists as opposed to published papers.
See, at the time, the journals (and the scientists) were under no allusions that it was the journals’ job to be the arbiters of correct and incorrect, the gatekeepers of what was scientific and unscientific. The point of the journals was to be the bulletin board of new science from around the world; they were a way to re-create the culture and knowledge-sharing of a departmental colloquium with scientists from around the world. Getting your paper in the Physical Review was nice because a lot of people read it, but I’ve never seen an account of a top scientist bragging that they got a paper in the Physical Review as an accomplishment in and of itself — and, speaking frankly, they brag about a lot. And when they got told to submit in one journal instead of another, like when Feynman got told by a referee at the Physical Review to maybe submit in the Review of Modern Physics instead, they didn’t seem to think it was a big deal.
This, in my opinion, was academic publishing in its most healthy and useful form. A field like physics:
Had researchers that more or less agreed on what compelling evidence looked like
Had quick and easy access to journals to share and consume new ideas
And its researchers understood that they had to read the papers in the journals and come to their own conclusions on how much they should trust the paper’s findings.
It seems that Feynman, whose memory is a little faulty, received less than a handful of revise and resubmits in his career. When asked him if he’d ever had any difficulties with referees, he replied:
Ever since the first paper, which is the Review of Modern Physics paper on path integrals, in which there was a small objection which I mentioned, there’s never been anything. I mean, I send it in and it gets published, just the way it is.
The reviewers seemed to quickly check the paper for egregious mistakes in math or logic as well as to give some brief commentary about whether they felt anybody had done this work before. And that was mostly it. From time to time, they did miss that a paper was repetitive or contained a mathematical error.
Feynman himself had a very strongly held personal reason that he didn’t review papers: how was he supposed to know if the other guy was wrong or he just didn’t get it? Feynman’s brilliance largely lay in his desire and ability to figure things out for himself. Oftentimes, he found it easier to use his own methods to work his way from an author’s premises to their conclusions than to follow the author’s logic step-by-step. Many times in Feynman’s own work, he knew for a fact that other researchers were not quite understanding what he was saying. And he was positive that he might be prone to this same error in understanding the work of others that seemed a bit off. He says:
Well, I started to try to look at the papers of other people but, you see, I have a funny thing. To me there’s an infinite amount of work involved. I would have to first understand how he’s thinking about it — not just understand the problem, but what he’s thinking about it. Then I’d have to go and see, is it Ok? Hm. Or what is it? I mean, it’s too much work, darn it. It’s like almost research: checking the ideas, seeing if it really works, and so on. It’s like research, and I can’t do somebody else’s research. I’m not built that way. I can’t think his way. I can’t follow and try to go through all these steps. If I want to worry about the problem, I read the paper to get the problem, and then maybe work it out some other way. But it’s too much work. Now, to read and just check steps — I can’t do it. And then, if a paper comes out that’s bad, that’s not very good, I’d feel very uncomfortable to say that there’s something the matter with it, or that it’s not OK, because maybe I’m not understanding. Maybe it is OK; maybe somebody else will see that it’s all right. I think it’s a lot of nonsense. Finally, I think most of the papers are a lot of nonsense and not worth publishing. And so, altogether it’s a miserable business, and I just say I won’t review any papers in order to simplify it because if I start reviewing some and not others, then it sounds like a criticism. There are a number of other things — I have resisted the outside world on this and a number of other things. For example, I never give commentary on whether a man is loyal or not loyal. You know this kind of investigation. And I got everybody off my back on that by just saying I won’t do it. And I never review papers. And one thing I would like not to have to do, but I can’t avoid, is writing recommendations for students. But after all, sometimes nobody else knows them, and they’re trying to get a job. So I have to do that. But I find it very distasteful. I don’t like to judge other people, or their work, at all. I don’t. I don’t want to judge somebody else’s work.
Feynman talked at length on many different occasions in the oral history about how, early in his career, the old guys like Bohr and Dirac just didn’t seem to get it in certain areas. They were guys he idolized since he was an undergrad and admired their contributions to the field, but he thought they weren’t really properly updating their thought processes as the field was developing — and it was developing rapidly. But, unlike today when issues like this come up in fields, he didn’t carry any malice towards them. They told him he was wrong; he told them they were wrong. It was friendly. This is how they debated. They had no power to affect his ability to share his ideas by, purposely or accidentally, influencing journal referees.
Feynman remembers a conference where one of these disagreements happened:
Feynman: Bohr was at this meeting and somewhere, after I’d tried and tried and I talked about trajectories, then I’d swing back — I was forced back all the time to explain. Finally I go back to the idea of an amplitude for each path; that quantum mechanics can be described by the amplitude for each path, and after that Bohr got up and he said, “Already in l9” — something, 1924, ‘25, or something –- “we know that the classical idea of the trajectory in a path is not a legitimate idea in quantum mechanics” and so on. In other words, he’s telling me about the uncertainty principle, you see, and so on. And when I hear this, this was the least discouraging of the criticisms, because it was patently clear that there was no communication, as you like to say. Because he’d tell me that I don’t know the uncertainty principle, and I’m not doing quantum mechanics right. Well, I know I’m doing quantum mechanics right, so there wasn’t any fear or anything. I mean, it was no trouble. It’s just that he didn’t understand at all. And I simply got a feeling of resignation. It’s very simple, I’ll have to publish this and so on, let them read it and study it, because it’s right. I wasn’t unhappy from that, you understand me? From Bohr’s criticism.
Weiner: Was there antagonism in this criticism?
Feynman: No. No, only the usual personalities. I mean, Teller, full of excitement, and Dirac mumbling “Is it unitary?” No, there was no trouble. It wasn’t antagonism. But to tell a guy that he doesn’t know quantum mechanics is to say, you know — It didn’t make me angry; it just made me realize he didn’t know what I was talking about. And it was hopeless to try to explain it further. And I said so. I gave up. I gave up completely, and I simply decided to publish it, because see, I knew it was OK.
The top physicists were (for the most part) friendly and respected each other a lot, but they could also argue with the tone of childhood friends. Here, they couldn’t agree, so the idea should get published for the whole community and they would go from there. That’s just how it worked.
Feynman on the open-mindedness of the physics profession at the time
Feynman generally found the conferences early in his career to be very useful. Just as in the scene described above, there was a lively give and take among the physicists and they felt comfortable and friendly enough with each other to be lighthearted and direct at the same time.
Above, Bohr was not being passive-aggressive or diminutive when he was saying that Feynman had forgotten basic laws of physics. Bohr, in fact, would make a point of setting private meetings with young Feynman at Los Alamos, going on long walks alone with Feynman because he valued his back and forth with the young man so much. This is just how they argued.
Also, in this era, it did not feel absurd to put forward theories that violated or replaced some new law or principle of quantum mechanics. After all, if you’re someone like Feynman or Schwinger and talk to the old heads of the field like Dirac and Bohr, and you know for a fact that you understand the recent developments better than they do, then it doesn’t feel that strange to think your additions to their theories might have some merit.
These conferences were a place where many people — even if not everybody — felt free to discuss new, hole-filled ideas out in the open. Here is an example from a 1956 Conference in Rochester:
I was rooming with a man at the time — Martin Block. So Martin Block said to me when we were going to bed, after the discussion of the experimental situation on this problem — he says, “All you guys worrying all the time about this Tau-Theta puzzle.” Tau-Theta, I guess it was called — there was a Theta meson and a Tau meson, now called the K meson. He said, “You know, from an experimental point of view, it’s very easy. It’s just the same particle. It’s only that your principle of conservation of parity is cockeyed.” He said to me, “What would be wrong with assuming that the conservation of parity is wrong?” So I said, “Well, let’s see. That would mean you could distinguish right and left, in a fundamental way, but there’s nothing the matter with that. I don’t see anything wrong with it. But I haven’t been involved in these things, and I’ll ask the experts tomorrow, hm.” So I said, “That’s a very good question, and you should ask the guys tomorrow.” So he said, “No, you ask them for me. They won’t even listen to me.” “All right,” I said, “Ok.” So I got up and I said, “I’m asking this question for Martin Block.” I’ve been teased a lot about that. People tease me on the grounds that I said that because I thought it was such a ridiculous idea. But it was quite the opposite. I said that because I wanted to establish the correct priority for the idea. I swear that. I mean, it was not because I thought it was silly, but because I thought it might be possible. And it was so good an idea, and might be possible at that time, that I wanted to be sure they knew where it came from. I said, “I ask this question for Martin Block. What goes wrong if you assume —” you know, that parity is not violated. And I think Lee answered it, or something. It was a long complicated answer that I didn’t understand. Then afterwards Block said, “What did he say?” And I said, “I don’t know, Martin, what he said. It seems to me still possible that parity is violated.”
To the people in the room who followed what was going on a little more closely than Feynman, apparently the idea felt a little far-fetched. Oppenheimer, once the group had discussed the idea for a bit and explored the possibility together, closed that bit of the discussion saying something like, “Well, I think it’s time to close our minds again.”
Block’s point, in the end, did turn out to be right. And the community deserves credit for their extreme openness to constantly examine the possibility that one of their new principles, which they were surely proud of, should possibly be replaced with something better or removed entirely.
There was a general sense of understanding in the physics community that the modern theories that physics rested upon, then about four decades old, had also felt absurd to the field when first proposed. So, a physicist should be careful when calling any idea silly before really thinking it over.
When Charles Weiner, the oral history interviewer, asked Feynman to expand on the rapport that he and Professor Wheeler had when Feynman was a graduate student — casually tossing frequently incorrect but always interesting ideas back and forth — Feynman said the following:
Yes. Well, what he did, you see, things like — I’d like to remark that the moment he mentioned advanced waves — that is, against causality and all this other stuff is against cause, the causes would precede the effect — no, the causes would follow the effects instead of preceding them, and so on — I didn’t ever say, “But that’s impossible!” or anything like that. I was not ever upset by any of the obvious troubles, as against some principle of causality or something. This was from the training we had in physics from Einstein and Bohr and so on. See, the history of physics was that a crazy idea like relativity, which is so evidently nutty — like when one man thinks two things are simultaneous, some other guy riding by doesn’t say so — or, that you can’t measure simultaneously position and momentum, or something — It had been discovering that you must always think carefully about the real experimental situation before you cavalierly say such a thing is impossible, you don’t like it. So I never objected to any of these crazy ideas, on those grounds. I never said, for instance, “How can it go backwards? How would it know when it’s going to meet an electron?” I knew that that was something we would have to study — that that wasn’t obviously cockeyed. The fact that there were protons and not positrons were an obvious trouble, but I let him get away with it, so someday we’ll discover how the protons go, wind up in this knot, too. But never mind. His brilliance, the wildness of his ideas, apparently impossible ideas, did fall on fertile soil, because I never objected to what other people would immediately have objected to, you know. All the books would say we can’t use advanced waves because this would mean effects would precede causes. But things like that never bothered me.
Feynman continued:
Feynman: Those didn’t bother me, until we would sit down and analyze and find out, this is necessarily against experiment. That was clear, that we always had to do that, because you see, it would be too easy to object — it was a lesson that you can’t object to Einstein’s ideas on Page 1 in spite of the fact that they look like they’re wrong. How can something shrink when it moves? Sit down and analyze if it’s not impossible. But it isn’t impossible, see? That we had learned. I’m telling you this because it shows something about the history of physics, the connection — that the lessons from these other men were just precisely that. Don’t take it too quick that it’s obviously wrong, just because it says something nutty, because you have to first make sure that the nuttiness is really nutty. In other words, take a real experiment; think very carefully that you will get an advanced effect that is directly opposed to what actually happened. When we tried to do that we didn’t get anywhere, see? We didn’t find such a thing. We got around all the paradox. So everything’s OK. So I know. These things never bothered me. And as soon as I tell people these ideas, they often come to me with all this, “Wait a minute, how’s it going to —” But I never had that trouble, in the beginning. The history…
Weiner: — was it a self-conscious reference to history, or an absorbed tradition?
Feynman: Probably an absorbed tradition. Just an absorbed tradition — that you know that nature can look very, very strange, in the fundamentals, and yet produce in the end the natural phenomena in a way, very different looking than you would think at first. It’s all right. You’ve got to think it out, you can’t just jump that it’s wrong.
Feynman on the declining usefulness of conferences
Towards the end of his career, Feynman felt that academic conferences were getting far too big and becoming less useful. To put a rough date on this transformation, around 1956 Feynman was still making positive remarks about the conferences happening such as the Martin Block Conference in the prior section. But by his final 1973 interview for the oral history, he seems to be making generally negative comments about the changes in conferences at the time.
The following excerpts, more or less, should give the reader a rough idea of Feynman’s thoughts on the changing state of conferences towards the back half of his career.
The series of conferences Feynman found most impressive were, by far, a series of small conferences in the immediate post-war period put together for a group of about 20 theoretical physicists. He recalls:
There were meetings of theoretical physicists, of relatively small groups, 20 theoretical physicists who would get together in different parts of the East. The first meeting was on Shelter Island, called the Shelter Island Conference, and there were some theoretical physicists, also Pauli. We were supposed to discuss the theoretical physics problems of the day. The Shelter Island Conference was my first conference with big men, you know, and I was invited there. Bethe was there, Oppenheimer was there, Pauli was there, Breit was there. Everybody of any importance in theoretical physics who was still alive and was around that part of the country was there. Now, where the money came from and who — Oppenheimer had a great deal to do with it, I think, in inviting the people and organizing the thing, somewhere, somehow. Money came from the National something. There was no National Science Foundation then? National something.
He continues:
Many of the problems of the day were discussed: puzzles about what the mu meson is, a suggestion by Marshak of an intermediate meson, a meson produced that disintegrates into mu, which was the pi-meson. A lot of exciting things were suggested and talked about. However, in spite of all this, they ran out of ideas. And they asked me if I wouldn’t explain my path integral way of doing quantum mechanics. So I did. Now, I must have been preparing my manuscript, or finishing writing the manuscript, because it was all organized, and if it had been before this time of working, I would have been so disintegrated (I hadn’t looked at anything) that I couldn’t have done it. So this gives us a certain amount of timing. All right. And I did OK. I explained it. Of course, it’s hard to pay attention to some new ideas, and they didn’t pay much attention I suppose. Then, at this conference or at a later one (and it’s an historical question, it’s easy to figure out) some questions about the Lamb shift business were suggested or measured or indicated, or somebody said they were going to measure it, or it had been indicated that there was some shift. And Schwinger claims to have said that he thought it was due to this electromagnetic energy shift that had been coming out infinity up to now. And I tried to estimate it by how much our damped oscillator shifted in its frequency, but I didn’t understand the real problem. Schwinger understood it better than I, and got too low a value by very many thousands. But Schwinger said that wasn’t the right way to figure it out. I remember this. See, this was up in the meeting that we were talking about it. I would estimate and say, “What’s the matter with this? It comes out too small.” He says, “No, no” — and so on, and so on. So there was some conference at which we discussed this question. And also there was a conference, but I think it was one later, in which it was indicated that the magnetic moment of the electron was not right, that the magnetic moment of the electron was not exactly the Dirac moment but was slightly corrected, and that this possibly was also an electromagnetic correction. Probably at the first conference, but possibly at the next conference, this went on. OK? So we were aware of the problems, and we were beginning to get, from Rabi’s group, some evidence that the magnetic moment was cockeyed, and from somewhere else some evidence that the Lamb shift existed. So that’s interesting and important to me, of course. These three conferences — as far as I can remember there were three conferences—were to me of very great interest and importance, and I was very unhappy when they ended. I asked Oppenheimer later why they ended when they ended, and it was, he said, because they were getting big. It was very difficult, after you invited somebody, not to invite him again. But people always had to be new ones because they were doing something experimental, they had reports, something — and it just began to grow. And there were too many insults, everybody was insulted, and everybody was writing, “Why didn’t you invite me? Why didn’t you invite me?” And he was sick and tired of it, and so he quit this thing. But this was a very important conference. There have been many conferences in the world since, but I’ve never felt any to be as important as this.
About seven years after the 1966 Feynman interviews where the above quotes were collected, Weiner followed up with Feynman for an additional interview. And Feynman had quite negative things to say about what he viewed as the decline in the usefulness of conferences in helping generate new ideas. His negative comments were, once again, related to the propensity of conferences to only grow in size:
Weiner: How are they [conferences] going from what you’ve seen over the years? Is this the same kind of continuing tradition of the same kinds of people coming together? Because in the early period — we talked about the meeting where you got up and said: “Mr. Block has an idea that I would like to tell you about,” and you talked at the following meeting on that, and these were very exciting things. Has it continued in that same tradition?
Feynman: No, they’ve gotten too big. For example, they have parallel sessions which they never had before. Parallel sessions means that more than one thing is going on at a time, in fact, usually three, sometimes four. And when I went to the meeting in Chicago, I was only there two days before I broke my kneecap, but I had a great deal of trouble making up my mind which of the parallel sessions I was going to miss. Sometimes I’d miss them both, but sometimes there were two things I would be interested in at the same time. These guys who organize this imagine that each guy is a specialist and only interested in one lousy corner of the field. It’s impossible really to go — so it’s just as if you went to half the meeting. Therefore half is not much better than nothing. You might as well stay home and read the reports.
Of course, Feynman’s is only one opinion and many things were changing in science at the time. However, he does seem to have accurately observed the trend of incentives/pressure towards research silos early on, which he thought was ridiculous, and pushed against it in his own work. This was not some over-the-hill physicist. In the early 1980s, about ten years after this interview, he would publish his famous quantum computing paper as well as the Feynman Lectures on Computation. If he was an old dog, he was one with many new tricks.
In an age when people feel it’s increasingly impossible to make novel discoveries in multiple areas, Feynman’s in-the-moment observations on how the research incentives were changing and his conscious decision to not give in to them should give us a lot to think about.
Until next time:)
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This reminds me of a post on the usefulness of peer review: https://open.substack.com/pub/experimentalhistory/p/the-rise-and-fall-of-peer-review
Feynman's mindset is a great example of Karl Popper's metaphysics concept, isn't it?