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In footnotes or endnotes please cite AIP interviews like this:
Interview of Philip W. Anderson by Alexei Kojevnikov on 1999 November 23,
Niels Bohr Library & Archives, American Institute of Physics,
College Park, MD USA,
For multiple citations, "AIP" is the preferred abbreviation for the location.
Discusses his childhood and education in Illinois, undergrad and graduate work at Harvard; writing his thesis with Van Vleck; working at Bell Laboratoreis and the scientists there including William Shockley; the rise of interest in solid state physics in the early 1950s; research in superconductivity; the creation of theory groups at Bell Labs in 1956 and the relationship between theorists and experimenters in the lab; decisions on research topics at Bell; his year in Japan with Kubo; security restrictions at Bell and military research; collaborations with John Galt; experiments leading to localization of electrons in 1956-57; development of superconductivity theory; his visit to the Soviet Union in 1958; collaboration with Morel in 1961 on superconductivity; and research philosophy and approach to problems. Others prominently mentioned are: N. Bogolyubov; George Feher, V. Ginzburg, Gorkov, Charles Kittel, Lev Landau, David Pines, Harry Suhl, Gregory Wannier.
It is November 23, 1999, and this is the third part of the interview with Phillip Anderson at Princeton.
I wanted to add to what I said last time about style. There is one aspect of my particular style of doing physics which I think is important. Perhaps it wasn't that unusual then; it's a little unusual now. And that was I've always taken experimental results and drawn theoretical conclusions from them. Fore instance the localization paper; I did the work because I was so firmly convinced that George Feher's experiments really demonstrated localization and that they were incompatible with conventional transport theory. This happened again and again. On the magnetic impurities, there was a clear dichotomy. There were some cases in which iron as an impurity in a metal has no moment, is not magnetic, and there were other cases where it was definitely was. The contrast between these two was experimentally so strong that I knew there had to be a real transition.
One thing I've noticed particularly about the theoretically trained physicists, of the younger generation: a feeling that the mathematics must contain everything, and that it's a little bit unfair to use experiments. They feel that you're cheating on the game if you look in the back of the book and look at the experimental data and draw fundamental theoretical conclusions from that. I feel that your are essentially twice as efficient if you can use both theoretical and experimental clues; understand the theory well enough to realize that a certain piece of experimental evidence is incompatible with the way people had been thinking. And often the experimental evidence looks to other people very amorphous—it's qualitative rather than quantitative. But the most important experimental evidence is the piece of evidence that no one else has picked up either because they take it for granted or because it's qualitative. A perfect example of that is Einstein's principle of equivalence. No one had ever noticed that the two masses were equivalent, that that was strange. But of course he deduced the entire theory of general relativity from this one fact. That experimental fact is more important than any amount of mathematics.
It was my impression there's also another difficulty in condensed matter physics. There's way too much experimental data and it is important to distinguish which experimental data have fundamental theoretical importance and which results from all sorts of particularities. And I was just wondering if you could try to explain what criteria here would be for you? Maybe with some kind of an example from your own work?
Well partly it's a matter of really looking at the experiments fairly carefully. Of course, early in my career I had the good fortune of working with really superb experimentalists like George Feher. Later on I came to differentiate between experimentalists and between types of experiments. A piece of bitter experience. I can remember feeling for instance, that vanadium sesqui oxide had to have a Mott metal insulator transition. I asked my friends who did neutron diffraction whether it was an anti-ferro magnet and they said no it's not, we don't see anything at all in that data. I learned that you don't trust neutron data until you've talked very extensively to very careful operatives, and asked them about possible errors.
And when was this?
That was when Frank Morin came around with these enormous jumps in conductivity (he published in about 1955?). Many of them were clearly not Mott transitions, but V203 certainly had one. Later, much later, it was the Bell Labs group that cleaned it up. It was the group of McWhan working with Rice, Brinkman and I don't remember who else, in 1970 or so, 15 years after my original guess that this was a Mott transition.
What does a Mott transition go to?
Philip Anderson on the bias that both experimental and theoretical physicists can place on their data sets.
(I don't think so ???. Probably.) Or people came to call it the Mott transition. Mott needed something to distinguish the Anderson transition from the Mott transition. He called the mobility edge and the metal insulator transition associated with the mobility edge, the Anderson transition. So he accepted the name that the rest of us had been using.
It requires taste and judgement, but it also requires knowing that a lot can go wrong with experiments. When you see one substance is a metal and another is an insulator, that difference isn't something that experimentalists can make a mistake on. I mean it's clear. If it's shiny it's a metal; if it's transparent it's an insulator. It isn't quite like that in the case of these substances but it was like black and white. In the modern era, when I'm worrying about high Tc super conductors, these are very complex materials. The number of mistakes you can make analyzing them is infinite. You need a great deal more experience and subtlety in understanding what experimentalists are telling you. There are other problems. Thanks to the success of the Bell Labs style, the Bell Labs method of working in teams of experimentalists and theorists together, that there is a tendency for every paper to have its own theoretical interpretation. You have to be very watchful to make sure that either the experimentalist himself or the theorist hasn't biased the presentation of the data. Very few people fake data, but very many people bias the presentation to bring out the points of the particular interpretation they make. Always my advice to young theorists is always don't look at what the experimentalist says about his data. Look at the actual points. Look at the actual experimental data. And then you'll, more than half the time, or a very appreciable fraction of the time, you will find that the points on his graphs don't say what the experimentalists says they say. They do not. They're interpretable in some entirely different way.
You mentioned the style of Bell Lab of experimental and theoretical as working together. But wasn't it exactly your generation that separated theoretical physics as an institutional group inside the Bell Labs in experimental?
Yes. Well both of these things happened more or less during the period that I was there. The post-war system, the post-war style was for there to be a house theorist for any given group of experimentalists. Herring and Gregory Wannier, for instance, were in the physical electronics group. Then there was the solid state physics group. And this was confirmed and led to the laboratory style by the success of the Bardeen-Brattin group. Bardine was a superb man at working with an experimentalists and thinking, asking the right questions about the experimentalists work and so on. And so we took that up. Later on I worked in this kind of teamwork with Feher and then later with Bob Shulman. In the first case on electronic magnetic resonance. Harry Sahl worked closely with Larry Walker. And there were many such teams. And the really good one, was Bardeen and Pearson who wrote the big review paper on covalent semiconductors before the transistor was in ???? the entire physics of germanium.
When you were working together with the experimentalists, was it reasonable for you to tell experimentalists what to do or to suggest going on a new path for trying things?
So who had the initiative, or had the upper hand?
Neither, neither. It was strictly cooperative. That was one of the, again, that's a real strength of the Bell Laboratories is the fact that nobody was anybody's boss. You did not work in large groups with a leader of the group and marching all in step with a leader and a group. Directly the opposite sociology from for instance modern molecular biology. When you ask a typical post-doc or junior scientist what he does, he would say, "Well, I work in Paul Berg's laboratory or I work in so and so's laboratory for some senior scientist," to whose credit almost everything that happens in that laboratory will accrue. Bell Labs, partly because they couldn't afford it because the individual scientist was so expensive and the overhead so crushing, so that a scientist costs three times what his salary was—his salary was much higher than that of a post-doc in the university. They couldn't afford to let the scientists be dominated, and so every scientist was free to break up any given collaboration and go off on his own. This happened to me again and again. By mutual agreement it happened to me and John Galt.
When was this?
That was '55 or '56. I think I already told you. It was not by mutual agreement that I stopped working with George Feher but because I got more fascinated by superconductivity. Although I didn't in the same sense work with Matthias to the extent that I was with George. But then later on I did get into this relationship with John Rowell on tunneling in superconductivity. And there was no sense in which John would do what I said or I would do what he said, necessarily.
How many experimental groups at a time could you possibly work with?
Oh that depends on how interested you were in other work. I worked at any given time intensively perhaps with one, but at the same time working with two or three others.
Was there some kind of a jealousy among theorists? For example, if you were working with a certain experimentalists' group, would it be possible for another theorist to start working with them at the same time?
I could tell myself that I'd usually welcome that. In fact in many cases— for instance when I happily transferred my responsibility from John Rowell off to Bill McMillin who came in as a post-doc. I think most of the senior theorists were deliriously happy if someone else came in and did, perhaps. There were a few jealousies and a few conflicts. There were very often conflicts between the experimentalists. There was a very good collaboration for instance for many years between Vince Jaccarino and Bob Shulman, and that one just exploded. Their personalities clashed. They alternated at giving the talks at meetings and being first author on papers. And then all of a sudden it blew up — because you never knew who was wrong and who was right. But one or the other had given his talk out of turn. One or the other was claiming the other's results were his own, and I'm sure both were at fault because I know both of them well and both are easily capable of being at fault.
These were two experimentalists.
These were two experimentalists.
Were there also conflicts between theorists?
Not so much. The worst case was Jim Phillips, who was a post-doc that we hired. He went off to Berkeley, but later on he came back to the Labs. As a post-doc he did very well. A very bad habit, about which he eventually became notorious in the laboratory, was taking one look at some experimentalist's data and saying, "Ah ha, I know all about that and I understand that perfectly." And he would then say, "Great we'll publish a pair of back to back Phys. Rev. letters." And the experimentalist would be flattered and thrilled to have this great theorist paying attention to his data and would say fine, fine. But Jim never gave very much thought to the experimental data, and very often his interpretation was premature or wrong or off the point, orthogonal to what the real issues were. He was notorious and people eventually had to be warned. I was involved in one of the first such cases.
What was the problem?
This was the first paper on the phonon spectroscopy, for understanding the interactions in superconductors. Tunneling measurements were done by John Rowell using what was then the rather new differentiating spectroscopy. He was differentiating the tunneling curves rather than just plotting current ??? voltage. He would see very sharp structure, and Jim took one look at this structure and said, "Ah ha! This is harmonics." He saw the peaks which were roughly in the ratio one, two, three, four. And said that's very significant, and jumped onto the paper and insisted on being a co-author on that paper. It was a very, very important paper, and the data were indeed very, very important. They were the origin of the phonon spectroscopy work. In fact the interpretation as harmonics masked the true interpretation which was that we were seeing the actual spectrum of phonons. We saw one peak for longitudinal phonons and one peak for transverse phonons. And then as the data got better we saw the actual structure of the density of states of longitudinal and transverse phonons. His interpretation was this is one phonon and then we've got just a bunch of harmonics. Yes you could see some harmonics later on. The nonlinearity was strong enough so that there was some harmonics structure. But that fundamental two-peak structure was the indication of what we were later going to be able to do, which is analyze which phonons precisely were the ones which were causing super conductivity and how much. I learned at last that this was a bad characteristic of Jim Phillips. Higher management actually never really felt sufficiently sensitive to this problem. It was just policed basically by word of mouth among the experimentalists. That was kind of jealousy that we had.
Well, but that's not a conflict right?
It was not a conflict. It was not a theorist-theorist conflict. It was a theorist-experimentalist conflict and it wasn't a conflict at the time. It just was a character defect that we came to know about. And he had a very distinguished career for 30 years doing the same thing. You know, most data that some miscellaneous experimentalist sees has not terribly much significance. And if somebody with a good imagination can see significance in it, the experimentalist is very grateful and he gets an extra citation. And so he became very popular with experimentalists of a certain type, and other experimentalists avoided him like the plague.
Did it ever happen to you, that you were involved in some kind of conflict?
No. Actually I managed to avoid most conflicts with other theorists. I had with management and then it wasn't a conflict with Jim; it was a conflict with management about their relative assessments.
But this was later.
Yes, that was much later.
So maybe we'll get to these points later.
It didn't become really severe.
So shall we go now to— Which would go first? About localized magnetic state or about the [??]?
Well let's see. Perhaps I should now do a little bit of history. In 1959 I went to about three meetings that year. Moscow, which I've told you about. I went to Cambridge to the superconductivity conference, and then later I went to a meeting at Oxford. Did I tell you that time I traveled by MATS, Military Air Transport System. Industrial people didn't usually have an excuse to do that but I was involved with a panel, a survey of solid state physics that was being organized by the National Academy. And this panel, this advisory committee in solid state physics—
When did you get involved with this panel?
I guess it must have happened about that time or a little earlier. So I actually had as a member of this panel an excuse of traveling on MATS because it was funded by the Air Force. They were very casually funded in those days, so I went to McGuire Air Force Base and island hopped it.
Just by yourself or I mean how many people would there be?
Oh no, I went by myself because there was this little discussion meeting in Oxford on magnetic metals. And I had these ideas on magnetic metals. This was the time, I believe when I had been doing some fairly hard thinking about magnetism and anti-ferromagnetism, super exchange. And either at this meeting or another magnetism meeting I made a notorious bet with Walter Marshall, who had just measured the hyper-fine interaction in the ferromagnetic metal Cobalt. He measured the size of the hyper-fine interaction, the size of the magnetic field on the nuclear moment. And I said to them, "I bet that's negative. I bet that's opposite to the electron moment." He said, "That's ridiculous." And he's talking in his very deep Welsh voice. He later became Lord Marshall. He was head of the Atomic Energy department. At that time he was I think head of the theory group at Harwell Laboratories and I guess I must have made this remark to him during my visit to Harwell at the time that I went to the Cambridge meeting.
Did you need any security clearance to visit Harwell?
No, no. I just walked in. They knew I was coming but I walked in. My daughter and wife came on their first visit to Cambridge, to England. And they went off and went motor-boating on the Thames, while I was visiting Harwell. And we drove off to the Southwest of England. Actually that was our first visit, and we still have a cottage in the southwest of England. So it was very important personally in that it became a love affair with the southwest of England. But I stopped at Harwell, talked with Walter, and made this bet with him that the hyper-fine field would be negative.
What did you bet?
One pound. And he later paid off and I made him sign a pound note. It's somewhere in my papers but I don't know where— Lord Marshall's signature on a pound note. Then I was invited to this Oxford discussion meeting where the food was very good because it was organized by Nicholas Kurti who was a famous physicist-chef. He gives lectures on physics and cuisine. It was a discussion meeting about magnetic metals and Andre Blandin was there discussing his and Friedel's concept of resonant states in metals.
It's important, let's talk about them.
So I heard there about this concept of resonances in metals and that Friedel was thinking vaguely of their occurrence in magnetic metals. But their ideas on this were very vague. And I stowed the concept away. Then the next year I went to the Utrecht meeting, and I told you about that. I also went to Toronto to the international low temperature physics meeting, where I talked about—
Do they meet annually there? Because there was a series of Toronto meetings?
Well this was one in the series of low temperature meetings. It's called ILT. This was number nine I believe. They had started in Oxford and Leyden right after the war and mostly transferred to the US. I went to very few of them because it wasn't really— I was a theoretical physicist more than I was a low temperature physicist. But I happened to go to that because I had something to say about superconductivity. It was a rapporteur session where I talked about Harry Suhl's work about magnetic impurities in super conductors. Harry Suhl had been working in one of our experimental theorists teams with Berndt Matthias on magnetic impurities in super conductors. He developed a theory of the affect of magnetic impurities in super conductors, which however was right in physics, right but in detail it was wrong. And that was the first meeting in the west where the theory of Gorkov and Abrikosov of the same phenomenon magnetic impurities in metals, was reported and it was actually reported in my rapporteur session. And I made one of my rather worst mistakes in that I said, "Well I think Suhl's theory is better although this seems to be saying the same thing." And it wasn't, and the Gorkov-Abrikosov theory was entirely correct and Suhl's was relatively primitive, although essentially right in the physical ideas that were in it.
So you said you were there like a reviewer.
I was a rapporteur, a reviewer. This is an official responsibility assigned by the meeting organization.
Did you need Suhl's permission to tell about his work?
No, no I didn't, of course.
Was it already published?
He submitted it as one of the papers for the rapporteur to summarize and it was already published in any case. I knew already about Harry's work and was interested in it. This was the background. Eventually through Matthias' urging, as a close friend, one of my very close group of friends at this time, he kept bugging me about why was it when he put various impurities into Yhrium, it was a very convenient case. When he put various impurities into Yhrium or when he put iron into Nobyldenum the transition temperature went down like a shot, just according to Suhl's theory. And then when he made an alloy of iron with rhodium it raised the transition temperature. It changed the band somewhat, but the iron wasn't magnetic at all. Its electrons just went into the bands. And this was one of those dichotomies and so I thought about it a while and I put together this set of experimental facts with this idea of Friedel's about resonant states and the magnetic impurities of the resonant state rather than the bound state of magnetic electrons in the metal. And I added to it my emphasis in the super exchange paper on the importance of the on-site interaction, the repulsive interaction on the same site. The Mott interaction, if you'd like. So I put all these three ingredients together and I came up with this theory of localized states and metals which is the...
...the 1961 paper. So that started out as an explanation of why some impurities were magnetic and some were not. And it came from the same kind of utter dichotomy that you found in the experimental data. It turns out, in fact in the end that it wasn't a dichotomy, that it was actually two limits of a re-normalization theory. But I certainly didn't know that at the time. What I did was to present a model and it is the cleanest and the simplest possible model, which in fact explains the physics of magnetic impurities in metals. And that model has had a life of it's own. At that time I had no idea that my dichotomy was going to turn into the Kondo effect, but eventually it did. Actually there had been an older history. It's various things I was puzzled about. The magnetic impurity problem in fact started with the Berkeley group, their measurements on—
Well the work on magnetic impurities started with the Berkeley group who had been doing electron, paramagnetic resonance on manganese impurities in copper, the substances which later became canonical spin glasses. And it had been hard to understand, you know, how do you define a magnetic impurity which is in contact with paramagnetic spins in the metal? How do you get a theory of the exchange interaction between the metallic electrons and the impurity electrons that the so called Kondo Hamiltonian or the Yoshida Hamiltonian , the models that my various friends from Japan had made for this kind of system. And so in a way I had been puzzling over this whole ball of wax for a number of years. And I was very satisfied and I was very happy that I could produce a model which had a certain amount of realism to it that adequately explained the various relationships between these different things, between the degree of localization of the moment and the interaction with the background electrons and so on. And also brought in this important concept of the resonant state that Friedel had brought in. And I kept puzzling, kept fiddling with that model for a number of years, as a matter of fact. There was a paper on a pair of interacting Anderson models by Schlomo, Alexander and myself. Schlomo came to work with me for a summer. There were papers in the Nottingham Magnetism meeting in '64. I went to the Nottingham Magnetism meeting and talked about the relationship between this and the Freedel sum rule, and then finally I actually talked very much about these resonant impurities in the long paper in the 1966 Varenna meeting. So I kept tinkering with this model, but the basic idea was there already in 1960 or '61. But it came out of this interaction with Suhl and Mattias and at the same time the ideas I began to form way back in that Brasenose meeting in Oxford in 1959.
It was at that Toronto meeting that Roger Elliot from Oxford and essentially at the same time or perhaps at another one of the superconductivity meetings, Brian Pippard from Cambridge approached me and asked me to come and spend a year's sabbatical, in one case at Oxford and the other case Cambridge. Roger actually, I believe, was first. I was very much intrigued by it because we'd visited Oxford and found it a lovely city and we liked Roger who visited our house. But Brian Pippard, whom I had known actually as a figure since way back in war time 1944, when I met him at that meeting in Washington, and I admired him very much, and actually I asked the two of them one question was really the only important question to me. I asked, "Could I give a lecture course?" And Roger Elliot said, "Well you could but I kind of doubt if anyone would come listen. It isn't the Oxford custom to have lecture courses on the graduate level, and in undergraduate education the system isn't something that you need to, or would like to, fool with." And Brian Pippard said, "We would be delighted if you gave such a lecture course, and we'll guarantee you that there will be an appreciative audience." And so I made the decision to go to Cambridge. I didn't know that at the time that Mott was very interested in my going. He was of course the boss of all—he was the Cavendish Professor and very important, very powerful in the entire politics of the University of Cambridge.
Did you know him before personally?
He came around— I guess I must have first met him in his visits to— oh, well of course I first met him in Japan. He was the Chairman of IUPAP (International Union of Pure and Applied Physics) and as such he was sponsor of the Japanese Kyoto meeting. And he was the man who always responded to the toast and gave the official speech and he was wonderful. He was at his zenith, you know, that was his period when he was on top of the world. He had this marvelous group at Bristol. He was just about to be made Cavendish Professor. He has this marvelous group in Bristol which had done wonderful work on dislocations and on physical metal (???) and so on. And he was just producing his famous papers on the Mott Transition, the Mott Phenomenon. So yes I knew him. And as a matter of fact, he happened to go on the same— there were post meeting tours that we all went on after the Japanese meeting. And we chose to take the post meeting tour to the north of Japan. And so we had a long train journey from ??? north to Hokeido. And I have a snapshot from those days of my daughter Susan sitting on Mott's lap, and he played with her and was very helpful with her for the whole trip. And of course he was at that time way above me. I hadn't done localization. But by 1961, of course, he had become very interested in localization, and he had come to Bell Labs and talked to a group of us about some of these things. He was mostly actually talking with Thorton Reed about the Frank Reed Dislocation Mechanism. But he's dropped in to the theory group and talked with a bunch of us about Mott Transitions. And that's when we got the Mott Transition from the horse's mouth. We were very interested in it. And he had become interested in localization. So although unbeknownst to me, he was pushing very hard to have me come to Cambridge.
Was he at that time also trying to redirect the Cavendish from nuclear physics to solid state?
Oh yes, he was in the midst of doing that.
Was it a difficult process?
Yes, I suppose so, but I knew nothing about all of this. I was too young, too innocent. I was delighted to see it happen. But he was doing it.
I don't know if you talked to him about these matters at that time or maybe just your feelings. What was the feeling at that time about solid state physics as a discipline? Or condensed matter? Was it at that time called solid state physics?
It was called solid state physics. That was the period— it was exactly that period of the famous talk by Brian Pippard at the IBM meeting on superconductivity in 1960. His talk called the Cat and the Cream, which was published I think later in Physics Today. And to which later on was one of the papers that made me think, made me believe that the paper I gave called More is Different was worth writing. I think it was 1960 that he wrote Cat and the Cream. And his thesis was that you might as well quit doing academic solid state physics because industry was so much efficient that they were going to lap up all of the cream before the poor helpless academic cat could achieve anything. So he was horrified by the efficiency of the IBM, Bell Labs, GE, juggernauts.
And how big did they grow by that time? Like the Bell Labs.
Well, in terms of—
Let's say just theorists.
Theorists, we were not so enormous. We never became bigger than ten to a dozen. And of that the theory group was eight or nine.
Now that's probably more than the best university can afford to pay in this field.
In this field, perhaps it was. (Note: Cambridge had Mott, Ziman, (???), G.I. Taylor, many particle theorists, many postdoc students). But on the other hand it seemed to us at the same time that, for instance, we were experiencing competition from La Jolla where Walter Kohn had gone which is now UCSD. Walter Kohn went to La Jolla, became the department chairman, and immediately started hiring away all of our best scientists from Bell Labs. And it wasn't long before he had hired away Berndt Matthias and George Feher and Harry Suhl. He had the beaches of La Jolla and the marvelous climate and the marvelous atmosphere. At that time it was a much smaller university and you had a feeling of an expansive world. And you had Nobel Prize winners like Harold Urey and future Nobel Prize winners like Maria Mayer and Joe Mayer that were a part of the social scene. It was very glamorous and rather fast social scene, it turned out. Very different from the puritanical and Victorian type social scene that we had at Bell Laboratories.
Could you explain perhaps the term puritanical and Victorian by some kind of example?
Well the fact is that nobody at Bell Labs ever got divorced. If you got divorced you left the Labs. Not because you had to, but because mostly we didn't fool around with each other's wives very much. There was true Puritanism. There was one forbidden thing, which was the AT&T looked from the very start very negatively about sexual contact between employees and employers, between bosses and subordinates, and particularly between the boss and the secretary or secretarial staff. And in fact there was a department chairman in Holmdel who was fired. I knew about it quite well because the secretary, who was definitely an unglamorous young lady, eventually became my secretary. So I knew about it. So in that sense there was Puritanism. I don't know how much subrosa fooling around there was, but people eventually when they got divorced they tended to leave. George Feher got divorced, left. Vince Jaccarino got divorced, remarried a colleague, and they both went to UC Santa Barbara. So it was just an atmosphere. We were normal people and we did the normal things, but we didn't do anything spectacular. Or even much divorce and remarriage.
So when do you think divorce became acceptable?
Oh, divorce was perfectly acceptable. It was just that one would feel subtly embarrassed in the social scene, you know, isolated. I don't know why people left, but they did. They tended to feel if I'm going to have a West Coast life style, I might as well have it on the West Coast. And so they tended to do that at that time. Later on, of course, things changed. There were a number of people much later who experimented with soft drugs and so on. But I don't think we ever had serious hard drug cases.
I know it's probably not the time, but maybe you would comment on your choice of going to a university to the academic scene later.
Well, 1960 was the time also.
You mentioned that you had many offers at that time.
Well I had some offers. I didn't have all that many, but I did have a very sound offer from Stanford, and Stanford was seriously recruiting me. They asked me to come out, give a set of lectures the Spring of 1960. They arranged it so that it was the time when the apricot trees were in bloom. I was very tempted, but Joyce was not. I guess I told you that she hadn't like the West Coast so much, and she didn't think— well, she didn't have any sense that I was seriously tempted. I was seriously tempted, but I certainly wasn't going without her. It was probably a very wise thing to not go. Stanford was a department which went through a period of deep trouble before recovering.
Was Bloch there at the time?
Yes he was, but it was very much dominated by Bill Fairbank and Leonard Schiff. Well, there were unfortunate things about it. In particular Bill Fairbank tended to treat his graduate students as free long-term labor. A typical Bill Fairbank, Ph.D was seven or eight years. He also had his rather wild projects, and some of them were not particularly— well, of course later on came the notorious but there were some that were equally bad that we knew about at that time. But, you know, there were factories on the West Coast. There was the University of Illinois, which was snapping up some of our best people. There was West Coast and other (Texas Instruments) semiconductor industries. So we did not feel that we were in such great shape. And there's the other aspect of Bell Labs physics, which I mentioned to you. That the groups were small, self-organized, never collaborators more than two or three. There might be a long list of collaborators but they would be people who essentially were staff or tactical assistants; not scientists. Of the scientists there would be only two or three and you couldn't hold a collaboration together unless the science stayed exciting. So we couldn't tell anybody what to do, so we had certain disadvantages and certain advantages. The Cat and the Cream was just a stupid paper.
Maybe Pippard was referring to the British rather than American realities.
Perhaps British realities. On the other hand Pippard has always been a professional pessimist and a man who could talk you into being a pessimist even under the most optimistic circumstances. You have to realize that at this time he had Brian Josephson for a graduate student. And at this time the science of molecular biology was being born in the Cavendish laboratory. And what the hell was he complaining about? But he complained. So I went. I had the good fortune that Churchill College had just been founded one year before. I was a second year— the second visiting fellow that they had had.
So you were actually a fellow of the College.
I was actually a fellow at Churchill College, among its first group of fellows, which were an extraordinary batch of people. Crick was still on the list although he had resigned over an argument about the chapel. Richard Keynes later became a Nobel Prize winner, I believe. Teddy Bullard. David Thouless was a fellow and a very junior fellow. I think he was a research fellow at the time. But there were a lot of people who were famous. The group that was doing molecular biology was very much well represented there and so on. And John Cockeroft was the master, a very, very sweet person who was very friendly to us. And so I have the dubious experience to dine in college and all that stuff.
So how did it feel?
Well it felt great. I mean I was young and drank port after dinner and all of that jazz, and went to feasts and was invited out to feasts.
Was it at the time when women were still not allowed?
Women were still not allowed. Joyce had to sit at home and eat Wheaties when I went out to dinner.
How often was that?
Oh not very often. Once a week at most, and usually less than that, but she was invited to a number of feasts in that first year, because as a young visiting fellow I would often be invited out to feasts, and then some other person would have the right to invite her too to a feast. I don't remember whether it was '67...I think it was '61 when we started right out with a feast which was on the occasion of the 70th birthday of the guy who had discovered the neutron.
Chadwick, who was a Cambridge person. And then thereafter it was not long before Newell Mott I think was knighted in that same year, and he had a feast for that. And that was important to me because he was quite ??? when he gave his speech of appreciation. He was saying, well, you know, he somehow managed to insert in there in the middle of his talk how pleased he was to have Phil Anderson, and maybe they could induce him to stay permanently. It was the first I had ever heard of it. I was basically offered a job from the podium of this feast at Sydney Sussex College. And thereafter the staff at least of the Cavendish paid much more attention to me as an individual. We had dinner in the master's lodge in Caius College. He was still head of a college. And had to learn how to eat prawns out of a brandy snifter, which you know Joyce as the guest of honor had to deal with the brandy snifter first, which was a rather frightening thing for her. She had no idea which implement to use and so on. But professionally what was important was of course I gave a set of lectures which were—
For graduate students?
For graduate students basically. Graduate students or undergraduates; and one undergraduate was sitting in one of those lectures namely Brian Josephson, whom I already knew about because of his discovery of the relativistic shift in the MOSS??? effect [?], which was already notorious. But he also came up to me. He was very shy of course in those days, shy even for an undergraduate. But he would come up to me afterwards and discuss what I had said. And usually had some correction or other to make. I had misspoken or something. So it wasn't a matter of his asking for further enlightenment. He was just correcting my caesuras. But he claims that I brought out this idea of broken symmetry in the final lectures of this series of lectures, which fascinated him. I guess I gave my lectures for the first two terms for Michaelmas and Winter term, and finished in March.
'62. And when I came back he brought me this sheet of paper on which he had the long complicated calculation of the current between two superconductors. And he said, "This comes out with a very interesting term, which if you're right about this, your concepts of broken symmetry, is a way of measuring the relative phase of two super conductors, and would you check it over." And it was god-awful mathematics because he had done it all in the original BCS formalism instead of in the new pretty new formalism that Nambu and I and other people had invented. Or even the Bogolynbov formalism. He wanted to use BCS because the original BCS paper had carefully kept track of particle number in detail, and so anyone couldn't question whether they were somehow introducing non-conservation of particle number in some obscure way. And he still seemed to get the term, although the calculation was much simpler when it was later repeated without that silly, rather meaningless condition. And it was so long that I only checked over one term, but one term was totally different in form from all the others. So that if that term was finite, it was finite. And so I checked it and said yes, there seems to be such a term. Then Josephson—
How old was he at the time?
Oh he must have been very, very young. He was a prodigy. He was a third-year undergraduate, but third-year undergraduates were normally 21. He would've been more like 18. I don't know exactly, 18 or 19. The custom in the tea room was for everyone in the Cavendish to come and stand in line for morning coffee and for afternoon tea. It was the way of socializing. The custom was that a group sat together, graduate students with senior people so that the graduate students would not form their own little tight social knot and work too much on their own. So he would normally sit at the table with Pippard and Mott and/or I would drop in to different tables. I like to sit with Pippard and Shoenberg who were good friends. Shoenberg arranged for our house. Shoenberg also was a very good friend. Sometimes I sat with other groups. Well, there was the MOND laboratory group, and so there would've been John Adkins, whom I knew well later in '67 and thereafter. And various other graduate students, but the topic at that table after a while was what were we to do with this idea of Josephson's, and we kicked it back and forth. Pippard claims that I was the first one who wrote down, to say, well, it seems to have the form J sino. Brian Josephson doesn't have quite the same memory.
...As I was saying that the Mond laboratory group, which would have include Shoenberg, Pippard, and some of the junior experimentalists and the graduate students because they would've insisted on the graduate students sitting with the senior people, sat together, and I often joined them, particularly in that period and we would talk about Josephson's idea and argue back and forth. Pippard was rather negative about it.
Negative in what sense? In usual pessimistic sense or—
Usual pessimistic sense. In fact it was he who insisted that he was not going to pay the page charges for a Phys Rev. letter; he was going to have it submitted to the new Journal Physics Letters, which didn't charge page charges. And he was a little dubious about whether it existed, and thought it was a bit controversial. But I tried to persuade him that this view of mine about broken symmetry was correct, although I didn't have a full understanding of what the Josephson Effect really was at that time. But I did understand that what he was seeing was a current that was proportional to sign 0. And although Josephson may have written it down, certainly I was the first person who ever said it to Brian Pippard, because Brian Pippard in his memoirs makes that statement that I was the first to say that, to write down the formula. And J = Josino, which is the Josephson formula.
On the other hand, the letter that Josephson wrote contained a lot in it that really was not—certainly didn't derive from our discussions. He found the obscure note in Gorkov's derivation of the Landan-Ginsbury equations, which said that the order of parameter changed with time according to the Josephson frequency or to the chemical potential, and applied that to his thing. And then he realized that it would be possible to synchronize this frequency with an external field, which involved an understanding of nonlinear dynamics, which was certainly extraordinary in a graduate student. I guess he was a first year graduate student at this time. This knowledge I'd only acquired because I happen to have worked with Harry Suhl on the nonlinear effects in ferromagnetic resonance. So I understood it when I read it, but I made no contribution to that. And in general, that letter is remarkably complete in expressing the various aspects of the phenomenon.
In the course of having written or thought about those last pages of my book, I had acquired or was in the course of acquiring a more fundamental knowledge and understanding of the nature of superconductivity and the nature of broken symmetry. I think I had the mathematics straight in my head already when I was doing the gauge invariance considerations.
You mean the symmetry breaking.
Symmetry breaking idea. And of course by the time I arrived at those words I had firmly decided that there were states which were superpositions of states with different numbers of particles.
I'm just wondering if we could look back and try to remember how this idea in broken symmetry developed both in your and maybe some other's papers. If we can do this sub-story separate for now.
Well broken symmetry developed in my mind from the work on anti-ferromagnetic and the anti-ferromagnetic ground state. The question which had been on the table since Bethe's calculations in '31 on the one dimensional anti-ferromagnetic had been whether anti-ferromagnetic order in the sense of two oppositely directed anti-ferromagnetic sub-lattices was even possible. And in my paper, I had solved that hard first step from the point of view of looking at the quantum fluctuations. Essentially this is obviously the classical ground state of such a system. But it might not be the quantum ground state, and certainly in one dimension isn't the quantum ground state. And I showed that the zero point fluctuations, the quantum fluctuations, diverged in one dimension and failed to diverge in three dimensions—converged in three dimensions. So one could define an anti-ferromagnetic ground state. And then I also realized that the very fact of the symmetry which made this a real question, the fact that the Hamiltonian was symmetric in the reversal of these magnetizations, essentially time reversal symmetry and also rotational symmetry in the simple models, the very fact of this required that there be a mode, a so-called Goldstone boson, which had zero frequency and zero mass in modern terminology. And so I made the connection between Goldstone bosons and the fact that the classical state broke the original quantum symmetry of the system. That was the point of view from which I started my work on superconductivity. I realized that the BCS theory broke a symmetry of the quantum field theory underlying the super conductor. Namely that there was a gauge symmetry of the wave function. The wave function could have arbitrary phase, but that this phase had become a classical variable and its quantum fluctuations became restricted in the BCS super conductor, became divergent in the BCS super conductor, and therefore one could define a phase and define a state with a fixed phase, which was essentially the BCS state although they had not expressed it in this way. The BCS state was expressed in language in which they somehow deliberately wrote the state down in the number conserving language, which meant that they wrote it down as a macro-canonical ensemble of all the possible phase states. But I argued in those early papers that it was more correct to introduce the phase as a macroscopic variable because then one could understand the structure of the excitation spectrum. And then in my second paper I showed that the Goldstone boson was not necessary in this case because of the existence of the gauge field of the photons, the electromagnetic gauge field which was coupled to the broken symmetry to the gauge symmetry of the wave function. So I first discovered the Goldstone boson in my own version of it and discovered also in my two papers on the gauge invariance problem, discovered that in spite of the broken symmetry there was not a Goldstone boson in this case. That one had a perfect gap because the Goldstone boson coupled with the photon ended up being a plasmon. So that in essence is the Higgs mechanism for creating mass out of non-mass.
And when did you have the idea that there might be something general about this procedure?
I didn't have the idea until I talked to a number of different people about particle physics. I was at this stage realizing that the phase was really a classical variable, and I made this remark that the anti-ferromagnetic order was a classical variable, and also the phase in super conductors was a classical variable. This was the thing which was picked up by Josephson and he looked for a way to measure the phase. Incidentally, I'm sure that if you looked deeply into his motivations it was his interest in paranormal phenomenon, which led him to be interested in ways in which weird things could happen due to quantum mechanics—ways in which you can actually study the strange phenomenon of quantum mechanics on the macroscopic level. So he was hoping that somehow this would tell him how to read minds, but that's really a speculation. That's why he picked up so quickly on this and worked so hard on it. In my humble opinion, and I think it may at least have something to do with it.
How did he express his interest in—
He didn't at that time. He was very shy.
So it was later.
It was much later, but he certainly had always had that interest.
He's certainly not the only physicist to make such a connection.
It was only in my insistence that the phase was a real classical variable that I was helpful in those discussions, and this is why I'm emphasizing that. I made it as a statement that its current is proportionate to sin 0 but it doesn't mean anything unless is a real variable, is a classical variable, and is one of those variables that you can measure and constrain externally. But I hadn't yet figured out how you constrain it externally. That's the sub-story about broken symmetry. The story up to this point.
Should we go further with it?
Let me finish the Josephson Effect. That summer I had to go back to the states quite early because my daughter was enrolled in a music camp, and we took her up to the music camp. And then I went back to the Bell Labs and talked to John Rowell, and I suggested that if he ever saw something strange at the origin of his tunneling curves, (he had been doing this quantum tunneling between two films of super conductor already and had been beginning his measurements on the phonon structure.) I suggested that he should look and see if he ever saw anything at the zero voltage that might be a zero voltage current peak. He said, "Well, I've seen some stuff but it's hard to find." About three months after that in late November or early December he called me up and he said, "Well, I've got a new batch of junctions. They're lower in thickness than the previous ones were. Bigger current, easier to measure. And I am seeing something at the origin. But I'm worried that it's just super conducting shorts. Maybe these are thinner interlayers that I've used before, and maybe they've broken through." And so I came down and the first thing I did was to take the refrigerator magnet off of his wall and wave it around and then his current went up and down like mad. Which was of course already in Brian Josephson's original letter that it would be highly sensitive to magnetic field. And then we invented about four tests for whether or not it was super conducting shorts. The most important was simply to run the voltage up and make sure that we could burn out the shorts. We had burned out the shorts and came back and there was no change in the current. A number of other...I don't remember what they all were but they convinced us that it was not shorts. And then we made a rough measurement of an interference curve, basically a Fresnel interference curve. And then we started to publish the paper. We measured the critical current. We had compared the critical current with the current above the gap voltage, which it was supposed to be comparable with. We found the critical current was very variable but it was always quite a bit lower, and I was puzzled about that. In a week or two, I made a trip into New York, thought about something or another, and then thought about it on the train in and out. And came up with the answer which was that this was noise, that there was noise interference with the current. And the reason that the noise was interfering with the current was that if there was current there was also coupling energy, that the current corresponded to a coupling energy. And I calculated this coupling energy, in about an hour or so on the back of the proverbial envelope, and we came up with a coupling energy being comparable with the noise energy that was going down his leads from the background.
I always wondered whether the proverbial envelope ever exists.
Sometimes it does and sometimes it doesn't; actually I used a lined pad. I always work on lined pads. When I often turn the paper over and do it on the back of the page of the lined pad. But the problem was that you could measure the noise voltage. It was much higher than thermal noise. If it had only been thermal noise he could have seen it on his previous junctions. So we put that in the letter. And in fact we put in my little theory about the energy. And then I realized that during the summer Brian Josephson had occupied himself mostly with writing a fellowship thesis for Trinity College. Because being a proper Cambridge man and a graduate of Trinity College, to him the world consisted—you know, if you think the view of the rest of the world, the United States from New York is restricted strictly to West 12th Street; the view of the world from the gates of Trinity College is even more restricted. And so to him it was more important that he get a research fellowship in Trinity College than that he have adequate priority in publication.
So his mode of publishing all of his thoughts on the Josephson Effect was in the fellowship thesis that he wrote for his college. Of which he made three copies. One was circulated around the Cavendish and one was submitted to Trinity College and I don't know where the third went... because I certainly didn't have it except that he'd made a copy. And as soon as we'd observed it and phoned him that we were seeing it, he sent it to me, then I realized that this fellowship thesis contained all the considerations about energy and coupling energy and so on that I had already written up and we published in the Phys Rev Letter. Nonetheless, if we're interested in priorities I should point out that the first mention of the coupling energy in public print is in the Phys Rev Letter. So we published some of those results. We should have known about them previously. I should have thought about them independently. I should have insisted that Brian send me a copy of his fellowship thesis. And one of the remarks that I made in that Phys Rev letter was corrected, I forget whether in proof or before we ever actually— or whether it was an erratum. One of the remarks was that the effective thickness of the junction was the penetration depth and not the junction thickness. And that correction incidentally came from Brian Josephson. There's no doubt. He wrote that to me. So he had understood all of the basic phenomenology of the Josephson Effect, almost all. I re-derived it all, published it in that letter, and we of course made the experimental discovery. The other thing I wanted to say about the Josephson Effect is that it's claimed even in some of my later reviews and certainly by Giaever in and some of his review articles that many other people had seen the Josephson Effect and ignored it. Some considerations that Bob Dynes once worked out about that show that probably nobody had. Because these junctions that John Rowell were looking at were unique.
They were the first junctions that had probably ever been produced at low enough impedance to produce a Josephson Effect above the likely noise in everybody's measuring apparatus. Nobody was using screened rooms at that time. So we would've probably had the only junction on which it could've been seen.
Would these have been produced at the Bell Labs?
Yes, of course. In fact John produced them himself, or Ian his technical assistant produced them himself. This was typical of Bell Labs work. It was nothing that couldn't have been done perfectly at a university by a graduate student. You know, there was nothing we were doing in those days that couldn't have perfectly well be done in a university by a graduate student. It just was because we were quicker and smarter and had better communication and so on. So the Cat and the Cream was just not true. For one thing, Bria Josephson had just lapped up the biggest piece of cream that was going.
For a year and a half I was very antsy about this problem, because Brian had written this fellowship thesis. He had not published a review paper or a summary paper; nothing but his Phys Rev Letter. I was very nervous about the Peter Principle, the famous principle of Merton that says to him that has shall be given. I was already pretty well known. Brian wasn't. If I went ahead and published everything I had and as fast as possible, that would have been my natural response if whoever had discovered this had done it in Stanford or in La Jolla. But Josephson was a student and was slow to publish, and I could have published the rest of this work before he did. So I gave it a number of talks, which were not true publication. I guess the first one was at a thing called the Midwestern Theoretical Physics Meeting. Then I used it as the basis for my lectures at the Ravello Summer school in the Spring of 1963. And that was my first publication, and even so it came out before Brian's first publication. It contained one extra detail. I have the Plasma Resonance, which is now called the Josephson Plasma Resonance. But it's the only thing about the Josephson effect that Josephson didn't invent. But otherwise it was essentially Josephson's fellowship thesis with quite a bit of philosophy about what the effect really meant. Which I don't know whether Brian considers that's relevant or not. But I don't pretend that this was the first publication of any of this material.
Now, during that year in Cambridge a number of particle physicists were around—In particular Steve Weinberg. I don't remember whether I heard it from Steve Weinberg himself or from other particle theorists, Richard Eden, whom I talked with rather regularly and was a good friend. And also I saw a lot of particle theorists around Bell Laboratory. We had people who were on the borderline between particle and condensed-matter theory like Brout. We had true particle theorists like John G. Taylor, who came and spent a Brueckner summer with us. We had Keith Brookner. And Geoffrey Goldstone, of course, was around Cambridge although you seldom saw him. Somehow I heard about the Goldstone boson, and I head about the dilemma that the Goldstone boson had zero mass. And so no one could invent a broken symmetry theory of anything. And Nambu had already spoken to us about his theory of the pion with Jona-Lasinia, a superconducting type theory of the masses of the nucleons and the relative masslessness of the pion. And people were looking for broken symmetry theories, but they were very disturbed about broken symmetry theories because of the fact that there were no zero masses around. There was this relatively small mass of the pion, but that was the only boson around with even approximately zero mass. And already the minute I heard about that I realized that I had a mechanism which prevented this and which didn't require a zero mass.
So was it at Cambridge or was it here?
I think I heard about Goldstone bosons in Cambridge already. And I think I may have even heard of it the summer before from John G. Taylor. But I think it was when I got back that I was talking a little more with Brout in particular and John G. Taylor, and also with John Ward who came around to the Bell Labs every once in a while. Then I realized that it really could be—
Now where was he from?
John Ward? He spent a lot of time in Australia. He was manic-depressive, and whenever he got depressed by running up against the hard problems of particle theory he would come to the Bell Labs and work on electron tubes for a while. He worked with Harry Suhl and John Pierce and so on. And so he would occasionally drop in to the theory group and we would hear some of the latest news from particle physics. He seemed to enjoy talking to me and we talked about some of these things. So I set to work and thought it all out and showed how the photon did mix with the collective exertions of the super conductor and make a plasmon and wrote it out. And that is the paper that I wrote about plasmon gauge invariance and mass. This was completed I think summer '62, but it was published in '63.
'63. So it was probably completed summer '62. Very little attention was paid to it except that in fact— well, Higgs reinvented it. In some ways the particle physicists tell me had less understanding; in some ways he had more. He certainly made a real model out of it where I had only a mechanism.
Did you, in your paper, make kind of a—
...about the Anderson-Higgs phenomenon, if I may use the word. In the paper that I wrote I definitely said people have been worried about the Goldstone boson in broken symmetry phenomena. The Goldstone boson is not necessary. Here is the possibility of removing the Goldstone boson, mixing it with a gauge boson, and ending up with zero mass. I even made the point that the graviton could even mix with a broken symmetry, I guess a tensor broken symmetry such as solid matter, and that you would get the equivalent of a finite mass particle. Actually what you get out of that is a gravitational instability, but the principle is the same. So I think I really understood the nature of the mechanism. At the last minute, somebody, some person whom I didn't thank but probably mentioned in the acknowledgments, did me the disfavor of pointing out that there was an earlier paper of Schwinger in which he said, "Well zero mass doesn't necessarily have to be in there in all possible field theories."
And that's Taylor, according to—
Taylor, yes, presumable it was John Taylor who pointed this out to me. And so I wrote the paper as though I had previously read Schwinger's paper, which I hadn't. I had had the idea way back in '60 before I had even heard of particle physics.
And you also thank Klauder in particular for correcting some misapprehensions.
I don't remember what they were. But John Klauder I would've talked to also.
He was at Bell Labs?
He was at Bell Labs. He was one of our post-docs in the group, eventually became an MTS.
What was the reaction if any by both particle theorists on this?
Zero. Now it turns out—
But it was published in the Phys Rev before the Journal split into several series.
Oh yeah. It was not published as a paper in the Condensed Matter Physics. It was published as a paper in Particle Physics. Brout paid attention to it. And he and Englert two years alter produced a model of symmetry breaking, which if you'll read carefully the summary of their work that t'Hooft and Veltrian give (Nobel Prize winner this year), they say that they took off very much from the Brout-Englert paper, and there's no way Brout was not perfectly aware of my work and I would be surprised if the Brout Englert paper doesn't reference it rather than Higgs or along with Higgs. So in fact it didn't fall completely on deaf ears. In fact it is in direct line to the recent Nobel Prize. I had not known this until I finally read t'Hooft's summary of his work for the Nobel Prize or someone else's summary. So I was rather surprised that in fact it didn't disappear into oblivion.
To get back to superconductivity, I wasn't really only interested in particle physics or even primarily interested in particle physics during this period. I talked last time in detail about our carrying on the work on phonon bumps and on identifying and pinning down the mechanism for ordinary superconductivity. And I was very much involved with that during this period, first working with Rowell. And I've written all that history down and Lillian Hoddeson has it in her History of Condensed Matter Physics in any case. But at the same time I was interested in continuing with the Josephson Effect and in particular I was stimulated by a misinterpreted paper by Parks to try to understand what really happens in very small metallic junctions. So there was a young man from Egypt named Dayem who was interested in— I don't remember why he was. He was from one of the more device oriented departments, but they were looking for devices I guess in this field. So he was willing to do some primitive lithography for me. We built a very thin bridge of super conductor, a V-shaped bridge. Two Vs meeting at a point. And showed that that had various Josephson properties and that in particular that we could get the AC Josephson Effect out of this. As a matter of fact it was much cleaner than the measurements of Shapiro on the AC Josephson Effect. And I think it is very similar to things on which they now do mensuration measurements on the Josephson Effect. I'm not sure. But anyhow those were the first clean measurements on the Josephson frequency relationship. I wanted someone to do various measurements, various of the other interference measurements that one could do. In particular I was interested in rotating a superconducting cylinder and then a metallic cylinder inside a Josephson loop or squid. But nobody around the Bell Labs was very interested in these essentially mensuration issues that we were into, so I wasn't able to stimulate anything in that regard. I stimulated some very primitive patents on superconducting circuitry, which if anyone ever produces a superconducting computer will be very useful, but I don't think they ever will. As a matter of fact, John and I were very careful to take out the crucial patents on the Josephson Junction, and our patents cover squids, slugs, all possible superconducting quantum interference devices. We were unable to get the Bell Laboratories to enforce any of these patents, and so they are all treated by everyone as if though they were in the public domain. Which annoyed John to no end. It didn't matter much to me.
How many patents did you take?
I have about three or four.
On this particular, on this—
No, no. Well, we have the central patent on the Josephson Junction and on all possible applications, which might not hold up against Josephson but the Dayem Bridge is also patented, and that would hold up against all possible point contact devices and all the known squids have point contact devices. So we would certainly have a right to license the entire squid industry, but Bell Labs just wasn't interested in enforcing such patents.
When did it start that you first developed the use?
Oh, very soon. Five or six years. As a matter of fact the first squid magnetic measurement was published in my magazine Physics by John Wheatley, and that was in 1965. So I know that it happened within four years. Wheatley was the founder of the SHE company, which was the first manufacturer of squids.
Did Bell Labs try to do anything in this direction?
No, no. They wouldn't. It was not a communications device, and Bell Labs felt that they were in the business of exploiting patents on communication devices and would be seen as a nasty monopoly if they were to patent something else. This was a culture that was impossible to eradicate from the Bell Laboratories until Lucent Technologies recently took over the Bell Laboratories and tore it up root and branch and fired everyone who had it in their bones.
It was the worst mistake that Bell Laboratories made in the post-divestment period. The other thing I was doing with regard to superconductivity was flux creep. We were of course interested— Bell Laboratories was in the process of inventing, as a matter of fact, the high field super-conducting magnet. In 1960 I believe, '59 and '60 that was one Matthias, Geballe, Gene Kuntzler, simply for dumb stubbornness insisted on seeing how much current and how big a magnetic field they could drive through a relatively high TC niobium-tin super-conducting wire, and made the remarkable discovery that it would withstand fields up to 50 or 60 kilowatt, which were available because Rick Bozorth had built such a magnet. And I was asked why this was, and of course the mythology in those days was that it was because of the Mendelessohn Sponge model. Because even nine years later, nobody in the West had really read and understood the Abrikosov fundamental paper on type two superconductivity. It was in those years '59 and '60 that first BB Goodman who was working in France, began to discuss Type III, and then finally the Abrikosov theory was understood and it was understood why these high field super conductors or high TC super conductors could also withstand high fields. Which had been a mythology in the profession that they couldn't. And the discovery was made not as a consequence of the theoretical work that had been done nine years earlier, which I should have told them about but didn't know about. But I did just because they insisted on doing a measurement.
So we became interested in magnetic fields and superconductors and critical currents. And a set of experiments were undertaken on critical currents by a young man, again in a device department. Young Kim, a young Korean. And Kim first did some experiments which were derivative from Gene's and others experiments at GE. But soon he developed his own configuration, which was a super conducting cylinder, and started studying critical currents on super conducting cylinders. And being a careful experimentalist, he looked at the current a little more carefully than Gene had and he came to the conclusion that it wasn't steady. He showed that the super conductor was not going to be super conducting forever. It changed a little bit and I took one look at the curve that he was seeing and said that's logarithmic—that current is varying as log t (time). It wasn't a serious phenomenon. The current was going to go on flowing for the age of the universe we estimated. But we could see the initial stages of the logarithm very clearly. And I thought about that a while and I said that's creep. Because of my background, and I had become more sophisticated in thinking about the Josephson Effect, thinking about the analogy between vortices and dislocations, between superconductivity and rigidity of solids, I realized that super conducting vortex lines could creep as well as dislocations creep. And I was conscious of the phenomenon of dislocation creep and logarithmic creep of metals. So I said the same thing is happening here, your dislocations are undergoing creep. I looked up the papers and I invented a kind of a model on the back of a scribbled piece of paper. On the back of an envelope I invented the theory which is in the paper about the motion of flux lines. Anderson and Kim.
The hard superconductivity?
Was the term hard superconductivity?
We invented the term Hard Superconductivity because we then realized that the reason for one of these high field magnets was that the materials were crummy and that the flux lines were pinned, and therefore they were creeping. And the ??? the ??? also made it mechanically hard. And we rapidly acquired the obvious corollary that if the materials were pure, the flux lines wouldn't be pinned and they would flow easily. So Kim went to work and demonstrated the phenomenon of flux flow separately. Kim plays hardball. Although in fact I believe that all of these ideas were developed together, it was only the flux creep one that he allowed me to be a co-author on and I was not a co-author on most of the rest. I guess on the final Reviews of Modern Physics paper; we wrote that together: Theory of the Motion of Abrikosov Flux Lines. But I didn't mind. That was fine and I was delighted. Kim was a very bright guy to work with and we've maintained friendly relationships.
And did he continue working at Bell Labs?
He did for a while, but then he became a department chairman at USC, the University of Southern California. And he was a little disillusioned because he was not allowed to boast. I think that was the Seattle meeting after I got back, the first Solid State physics meeting, March meeting, after I got back from Cambridge. And we had a lot to talk about, and Kim in particular had a lot to talk about and we wanted to do a press release on this flux creep. The management said no you will not. We have made this wonderful discovery of super- conducting magnets and the flow of super-conducting critical currents in the presence of very high magnetic fields, and we don't want anything to detract. We don't want people to think that it's not forever. So Matthias went to his friend Geballe and vetoed our doing a press release. Kim was disappointed because it was his own university, the University of Washington.
I was just wondering whether Bell Labs had such an authority to veto it?
It had no authority to veto the work or the publication.
In scientific fields.
Yes, but they could put high pressure on about publicity. They thought Kim was telling this as too important a discovery, and so they could say well we don't really approve of your making a press release of this. Even though it was his own— he was a graduate of the University of the Washington, and he very much wanted to make a splash back home. So he was very disappointed and he did leave the labs with bitter feelings.
Otherwise was it Bell Labs who handled the press releases? Or who was responsible for publicity?
They certainly had to cooperate with press releases. If a comparable discovery had been made at most laboratories, they would've been happy to be out there waving the flag. It left me a little bitter, frankly, because I had made a sequence of very important discoveries. The Josephson Effect, flux creep. On a smaller scale we had the phonon bumps. Publicity on these things was absolutely zero. The patent protection was absolutely zero. I had the feeling that they were happy enough for me to go on working and doing physics as well as I wanted and as long as I wanted, but that the more empirical Matthias approach was getting a much greater degree of approval at the administrative level. And so I never felt quite the same about the Bell Labs after that.
Who was at the head of administration?
In our group, of course, the administration was fine. I had been incidentally department chairman in '59 to '61. Mel Lax took over then. He was retained for I think three or four years, and then after it was Peter Wolff. And they were very excellent advocates, and of course my salary went up. I got this very good financial deal on taking a sabbatical. It wasn't a true sabbatical. They paid me all the way through, and I had full benefit coverage through that whole period. It counted in the end for my retirement. So they treated me financially very well. But I think that my extreme loyalty to the laboratories weakened very considerably at that time. On the other hand, they were still supporting our group very well. At a higher level there would've been— well, it was the same people who had made the theory group. It was the group, the sequence of White and Baker. It wasn't until Ted Geballe was passed over for director of physical research and the job was given to Al Clogston.
Did you try to make them enforce the patent?
We spoke gently to them a couple of times.
To Hannay, for instance. Hannay was a very good friend. He was part of the gang. You know, these were friends also and we were being treated very liberally, being allowed to do very much what we liked. Of course the later Bell Labs, they would've been very happy with these discoveries because they were very important practically. But they would've been much more controlling of the research that we would have done. So I couldn't have found the Dayems and the Kims to do my bidding or work out my ideas the way I did. So in some ways, well, it certainly had a strong influence on whether I eventually stayed 100% at Bell Laboratories or not. Incidentally, one of the reasons that I went to Cambridge was that I felt after turning Stanford down that if I didn't go to Cambridge, I was never going to do anything exciting at all. So we decided we'd go to Cambridge, and that would relieve the monotony of being at Bell Labs. Okay that's probably time.
That's the end of a certain period.