Interview with Kenneth G. Wilson, part III

PoS

But for the 1971 papers, do you recall more about the reaction to these two papers?

KGW

There were the discussions I had with Michael, who was very impressed, he was more impressed than I am because he knew how long the field has struggled without being able to calculate anything. But at the time it seemed to be an incremental step forward for me and I did not think of it as a big thing. Whereas Michael was much more aware of its significance, but that's only after Michael comes back to Cornell. He was not there during the time of the seminars. But Michael and I started having intense discussions as soon as he came back. And of course, Franz Wegner came to Cornell and immediately picked up what's going on. I don't remember anybody else. And it was a short window, remember, before the epsilon expansion and the epsilon expansion has the big impact because that requires no computing.

PoS

But it's clear to Fisher fairly quickly that you supplied something that Kadanoff and Domb didn't seem to have.

KGW

Oh, yes. Fisher sees that instantly.

PoS

When does Wegner come actually?

KGW

It was right in that period. I couldn't tell you when he actually came... I suspect he came before the epsilon expansion papers. What I remember is that as soon as he sees these 1971 papers, he almost immediately comes and there's no question he immediately understood what they're about.

PoS

What's the relation between the 1971 papers and the epsilon expansion?

KGW

Once Michael Fisher comes back, we start intensive discussion of what's going on. And it's in a discussion in his office where we both come to realize that the key question is what happens as we approach four-dimensions. I offered to work out the expansion about four dimensions because it was an easy thing to do. I did the actual calculations. But my memory is that it was Michael that drives the discussion towards the question about four dimensions. All that I know is that as soon as it became a question of calculating things, then I go off and calculate. Remember the first thing that happens is that I have to do the calculations with the phase space cell approximation. And that's something I can do analytically. It's very easy. I do it finding out that four dimensions is the point at which the non-perturbative solution separates from the Landau-Ginzberg solution. Everything becomes perturbative as long as you're around four dimensions and not around three and then I could do the expansion just for the phase space approximation itself. And then, as a second stage, I realize that using the field theory, I don't have to do the phase space cell, I can do it for the full field theory solved in perturbation theory.

PoS

And at what stage do you realize which Feynman diagrams to look at and neglect everything else?

KGW

Well, that was essentially instantaneous. I mean I know so much about the diagrams at this point that it's a very quick process of doing the low order calculations and finding out which diagrams matter. Since I know the coupling is going to be of the order epsilon, i.e., small, all the field theory apparatus for perturbation theory applies in a very straightforward way.

PoS

And looking at the Kondo effect at that stage, does the stimulation for that come from Phil Anderson?

KGW

No. It comes from my utter astonishment at the capabilities of the Hewlett-Packard pocket calculator, the one that does exponents and cosines. And I buy this thing and I can't take my eyes off it and I have to figure out something that I can actually do that would somehow enable me to have fun with this calculator. And at the same time, and surely through Wilkins, I learn about the Kondo problem, and discover that it is very similar to the static model of the nucleon that I had been working on for many years.

PoS

The static model?

KGW

The fixed source models. The Kondo problem is just another example of a fixed source model. What happened was that I worked out a very simple version of a very compressed version of the Kondo problem, which I could run on a pocket calculator. And then I realize that this was something I could set up with a serious calculation on a big computer to be quantitatively accurate. And all the difference was the size of the gap between momentum slices. Unfortunately, I made a big mistake when I wrote up my work on the Kondo problem by not discussing the very simple limit that results from putting big gaps between momentum slices -- the simple limit that anyone could compute on a pocket calculator.

PoS

Why was it a big mistake to not put this simple calculation in the paper?

KGW

Oh, because almost nobody understood it. The interesting thing is in the past couple of years, a similar situation has arisen with the concept of renormalization group limit cycle. I first became aware of the whole limit cycle problem when Bob Perry, who was at Cornell, called my attention to calculations that had been done on the nuclear three-body problem with delta function potentials. And these are quite complex calculations and Perry was very puzzled by the ways things were coming out. I looked at what he was describing and I said, "That's a limit cycle." And almost nobody had thought that way before. Even though the results had been in the literature for thirty years. There's a quite complex integral equation you need to solve, and at that point, they only had the leading order solution. They didn't really carry it much beyond that. It became very clear that the people working on the three body problem needed a simple example of a limit cycle so they could understand what it's about. By that time, this was only three years ago, I knew I had made a big mistake in not giving people the simple version of the Kondo problem so they could see what was going on. Here Stan Glazek and I made sure that a simple model with a limit cycle solution was published and easily accessible to workers in nucleon physics.

PoS

Two quick questions. I didn't get all the inputs that went into the epsilon expansion. You were talking to Fisher?

KGW

Yes.

PoS

Were you drawing consciously on work that's being done by other physicists on similar problems?

KGW

I was just focused, in this case, on the field theoretic version of the Ising model. But I was using continuum variables, not plus or minus one, for the phase space cell approximation, which means it's the same as the phi^4 field theory. As soon as Fisher and I identify that four dimensions is the problem, as soon as I've done the calculation with the phase space cell approximation and seen how it works there, then I realized I knew how to do this by field theory. Just by Feynman diagrams. I've had ten years of experience; it was automatic to do Feynman calculations. Completely automatic. I did not have to ask anybody.

PoS

In arbitrary dimensions....

KGW

But once you write it as a Feynman diagram, you just set it up with d as a parameter and of course you have to figure out how to do it fractionally, and I don't know if dimensional regularization existed at that time or not, but I assume that if it didn't, it was going to come out very soon.

PoS

Whether it did or not, you weren't reading that?

KGW

If it came out, I knew about it. There, you can look at the paper, because if dimensional regularization were already out, I would've referred to it I think in the paper. It's a trivial matter to put in d as a variable because of the way Feynman diagrams are calculated. The way Feynman diagrams are calculated, all integrations are reduced to Gaussian integrals over the momentum and it's trivial of course to extend a Gaussian integral over a momentum to a fractional dimension.

PoS

Do I understand correctly that it was Wilkins who suggested you look at the Kondo problem?

KGW

I'm pretty sure that I learned about that from Wilkins, but there should be an acknowledgement of this in the papers on the Kondo problem.

PoS

Do you know how that came about? That he suggested it?

KGW

It really was just in a conversation with Wilkins, that the Kondo problem came up. I don't think there was any other way I would have learned about it except through Wilkins.

PoS

And that's already after the 1971 paper. Would it be your second trip to Russia, but before the publication of the 1974 big Kondo paper. Did you ever talk on the Kondo problem with Alexei Abrikosov?

KGW

That I just don't remember.

PoS

And in terms of going beyond what you had done, you would point to Wegner....

KGW

You mean in terms of how the field develops. Clearly, Wegner plays a very critical role introducing the concept of relevant and irrelevant operators and Wegner and Kadanoff do the statistical mechanics version of operator product expansion. And that, as far as I know, has no dependence on my on operator product expansion work. As far as I know, their work was totally independent.

PoS

But Wegner, presumably, had heard you about operator expansion and things like that.

KGW

I doubt it, because my paper was written for field theorists.

PoS

And the connection between you and E. Brezin and J. C. Le Guillou and J. Zinn-Justin...

KGW

That's because I went to Princeton in 1972 for the spring and gave a series of lectures and Brezin was there. I think there were two people, at the time at Princeton, Brezin and [D. J.] Wallace I think was the other person....

PoS

I have to ask, you wouldn't happen to have those lectures?

KGW

John Kogut wrote up the lectures and they are published in Physics Reports with Kogut and myself as authors.

[Break]

KGW

I think that one of the things that you want to do, in terms of the period before 1972, is to work on Holton's concept of thematic presuppositions. When people started into their research before 1972, what were the presuppositions that they had in mind? How did these change as they proceeded in their research, how much change took place? Because it's very clear to me that when I started research, I didn't know anything. So all I had were some presuppositions. I'm going through graduate school, and I'm trying to face a problem. I have to do something. And my presuppositions tended to be mostly questions about what approach I should take. I developed a presupposition that I should focus on field theory, after trying out S-matrix theory and figuring that S-matrix theory wasn't going to get anywhere, I thought I should do field theory. Of course, the quark theory came along, and I paid no attention to it. And in the end I didn't pay a penalty for not giving attention to quarks, but at the same time it was clear the whole field made a big mistake by not taking quarks seriously sooner than it did.

The whole reason for the whole field not taking quarks seriously, only a small fraction of it, is that the history of physics has not been analyzed properly yet, and the results are not yet part of the training of physicists. The history of physics is that the assumptions we make about when you can ignore research, like the quark research, are ridiculous, absurd. It comes back to this whole way of doing probabilities called Bayesian analysis. The whole idea is ridiculous. Because you go into research on something you know basically nothing about, and yet you assume you already know a lot about it, and that's the way people operate. What happened when the quark hypothesis came out was that virtually everyone knew the first version of Zweig could not work, because it violated the spin statistics theorem. But as soon as it had been figured out that all you had to do was to have three versions, the three colors, to avoid the spin-statistics problem, you were over the hump. There was no excuse anymore for not considering it, and the reason that it was so disparaged, even after that, was because people didn't know the history of physics, and they didn't realize that once you're dealing with a situation where you don't know what's what, you should allow for all kinds of alternatives. But we don't train physicists to do that.

PoS

Right, I mean, that's a philosophical dictum. You're not taking into account the context in terms of which people are trained, their positivistic and operational assumptions, etc, etc.

PoS

He's echoing an earlier debate between Ernst Mach and Max Planck, where Planck took the position that history sometimes gets in the way of making the next move, whereas Mach was saying, No, history is a resource for making the next move.

KGW

But you see, the problem is they haven't analyzed the physics. It's not simply knowing the history. It's knowing, for example, that it's happened over and over again that there has been a large or small parameter. That is the rule and not the exception. But I wrote a stupid paper saying that it wasn't natural to have scalar fields with a small parameter. And now, of course, we're discussing having a scalar field with an astonishingly small parameter attached to it, namely, the cosmological constant. And what is stupid about my paper is that if I had known about the whole history of physics, I would have known that it has happened often enough that a parameter that you needed to be large or small was large or small. It's happened often enough so you can't use the need for a large or small constant (as an argument against somebody’s hypothesis), it's not a justified assumption.

PoS

If you were to tell your story in terms of how your presuppositions changed, how would that go? Just as a first draft.

KGW

First of all I would start the story with the mathematical talent I demonstrated clearly at a very early stage. But I concluded I didn't want to go into mathematics. There were some people who wanted me to go into mathematics, but I didn't want to do that. I wanted to have something with a connection to the real world. Of course my father was a chemist, but he had done mathematics and physics on his way to becoming a chemist, and I decided I wanted to do physics because that was close to mathematics, but it was connected to the real world, and I've never regretted that decision. And of course, having an interest in all kinds of approximations, I didn't understand at the beginning just how powerful that focus would be for a career in physics. It was just an interest.

PoS

What about the contrasting supposition that you can have ultimate equations providing descriptions which are possibly exact, but you can only get approximate results out of them?

KGW

There was a long build-up to the point where I got that kind of sensitivity to the whole structure of the physical laws and so forth. When I was in graduate school, I was just taking subjects...

PoS

Did you see, for example, quantum mechanics and statistical mechanics as separate pieces of physical descriptions? Did you think that there was a connection between the two? The notion that somehow everything could be unified was something that even Feynman believed at some stage.

KGW

When I was in graduate school I had no sense of that whatsoever. There were these topics that you learned about, you were given a syllabus, and then as a graduate student I had to figure out what to go into, and it wasn't clear in my mind whether I should do field theory or something else. After spending a summer doing plasma physics and finding I had a huge amount of stuff to write up at the end of the summer, I said I don't want any part of that. I want to do something where it'll take me a very long time before I have to write a paper. And it became clear that field theory was the right thing to go into to have that kind of experience. And once I made that decision, I wasn't paying attention to [unification of different domains]. However, by the late 1960s I started noticing areas that were really hot outside of physics. When the discovery of the pulsars come out, I would run over to each colloquium on pulsars. Big results were coming out of Arecibo, which is run by Cornell.

PoS

So at the end of the summer you knew that you didn't want to do plasma physics, but rather field theory, in part because that would take a long time. Is that an assessment that the solution of such problems would be much more important than solutions in plasma physics in some ways?

KGW

It's not an assessment of how important it was. All I was concerned about at that time was having something that I could spend a long time working on. I just didn't like the idea that after only three months I had to write something up. It's just not what I wanted.

PoS

For the time being, we're talking about very general things, right? When do problems of phase transitions come to your attention -- just in terms of the kinds of presuppositions that might draw someone in that direction?

KGW

I wasn't even connected to the problem of phase transitions until 1965. But as I said, I would start with the presuppositions that led me into physics rather than mathematics; and then, in physics, the presuppositions that led me into high-energy versus another area of physics; and then the presuppositions that led me to focus on field theory rather than S-matrix theory or anything else. I wasn't bothered by the fact that this wasn't the hot area at the time. Then the presupposition that there was nothing I really had to pay attention to about the quarks when the quark idea came along. I was among the last people to climb on board the quark idea which happened at the time quantum chromodynamics was proposed and it became clear I had to learn about the quarks and the gauge theory. Then I developed the presupposition as I came to work on renormalization group that the Beta function would always have the wrong sign. There's a paper that I wrote in 1971 about renormalization group and field theory, and I discuss various alternatives for the Beta function, omit the one case that turns out to be correct. I don't mention asymptotic freedom as a possibility because I hadn't worked on gauge theories, and I just took for granted that the Beta functions would have the other sign. So that's where I wandered into a presupposition which was actually wrong.

But then I think it's legitimate to ask, once I got into the critical phenomena, what kind of presuppositions did I start with, and how did they change? And what I would say that a really very important thing which did not become a presupposition but became a question was this question whether the renormalization group with an infinite number of parameters was something that was workable. Would there be a convergence process so that the bulk of the transformation would apply to some finite subset of those infinite parameters rather than all the infinite number of parameters? There had to be some kind of convergence process where, as you increase the number of parameters, you can get more accuracy so that you never, strictly speaking, had to deal with the infinite set. And there I did not develop a presupposition instead. I wanted to have an example where I could demonstrate that it would not be a problem. I made a big investment and effort in order to establish that. So I think the really important presuppositions come earlier, but by the time I'm looking at the statistical mechanics, I've sort of become flexible enough. Does that make sense to you?

PoS

What I hear is a mixture on the one hand of psychological dispositions which make you look at problems in certain ways: hunches and conjectures about which way things would go, figuring out what tools and powers you have available to test certain models and make analyses and things like that. The fact that you think in terms of approximation and what will justify a particular approximation -- that's a very interesting kind of presupposition to try and figure out. Paul Martin likewise talks about that, but he may have a very different idea in terms of what you have in mind. So for example, being able to put it on a machine and compute it, I don't think that is something that crossed his mind at that stage. These are the kinds of collective presuppositions that you might help us clarify.

What is the impact of universality as a feature when it is advanced by Kadanoff and others? Is that something which is now collective to most of the people who are working in the field? It has been established experimentally, and there's sufficient theoretical warrant in terms of Domb's work and Fisher's work. Is this now a fact which must be explained? The same question with regard to scaling. At what stage does it become clear that scaling has become a shared presupposition, something that you have to account for in any adequate solution?

KGW

Clearly what you see in the 1960s is the recognition that scaling and universality are associated with the Landau theory, with classical theories of various kinds. And the recognition that the concept of scaling arises, in a sense, as a departure from classical theory, and yet still carries scaling with it. That's what people are concerned about. It's not classical, it's not Landau-Ginzburg, but then they have these relations between exponents and the scaling form for the equations of state and so forth.

The universality, of course, is trivial if you just have Landau-Ginzburg theory again. But in actuality you have a form of universality that persists in the presence of non-classical exponents. Part of the attraction of the renormalization group is that it allows you to explain these things. It's built into the calculations that you're going to get this particular form of universality, and the whole formalism will now tell you what is in the same universality class with what. But from my perspective, none of that was of any interest to me. I just wanted to use the critical phenomena as a laboratory in which to develop appropriate methods of computation that I could apply to field theory. Hence I was not concerned about the presuppositions of the people in critical phenomena until 1971, when I could address the concerns of the people in critical phenomena.

PoS

Very interesting. Yours is primarily a methodological interest. Given your presuppositions about what would constitute a solution, when is it clear to you that you essentially have a solution to the problem?

KGW

When I was first doing work as a postdoc I had dreams of glory. But by the time I finished the postdoc, those dreams were gone. By the time I produced the work in 1971, to me that was a small step. I was used to having some kind of mental breakthrough every few months or so, and this was just another one along the way. Michael Fisher was the one who saw that this was a very powerful insight for critical phenomena. That's not the way I was thinking. I was thinking I've made one step further in building my little laboratory. And then the epsilon-expansion -- you know, I did that because it was easy to do. It was sort of a trivial extension compared to what I had already done. And it never occurred to me that there was going to be a huge difference between impact of the phase-space-cell approximation and the epsilon expansion, just because the latter doesn't require a computer. And of course it's more than that, it has a very wide range of applications. The phase-space-cell approximation doesn't have the power that the epsilon expansion had. And at the same time, while I'm focused on calculating and getting approximations, I produced the 1969 paper in field theory where I do exactly the thing I hate doing -- I just make a set of assumptions, but with no way of calculating.

PoS

The first time that you and I met, you gave me a copy of Fisher's review, called "Renormalization group theory: Its basis and formulation in statistical physics." Do you remember that article? Do you think it captures the whole story of the development of renormalization group?

KGW

It doesn't capture everything, because of course he's not concerned with the work I did in field theory. Fisher says fairly explicitly that "renormalization group" is a misnomer. It's not related to the work of Gell-Mann-Low.

In retrospect, I probably made a mistake in giving it the same name. I probably should have given a name to distinguish the approach with one coupling and the approach with infinite couplings. At least I should have done something so that even if at some level you said everything was renormalization group, Gell-Mann - Low was renormalization group A and my work was renormalization group B. We would have gotten away from the arguments about everything reducing to perturbative renormalization group theory. Which is where the real confusion exists, between the stuff that you can do based on perturbation theory and the stuff where you have to set it up from scratch, with infinite numbers of couplings. And on that point, I think Fisher makes his point and is very reasonable.

PoS

Once you have established this little laboratory, how do you see your presuppositions changing in terms of your own general program after 1972-73?

KGW

Then the focus shifts. There's the short interval where I'm doing the Kondo problem, and that's a situation where there's a big payoff from doing the infinite number of couplings version of the renormalization group. There are quite accurate numbers coming out the other end. So I'm further establishing in my own mind that it's the infinite coupling version of the renormalization group that really counts. But then of course I get switched back into field theory. The big breakthrough happens in field theory, that asymptotic freedom with quarks + gluons is clearly what explains strong interactions. Once the articles come out on that there's no question in my mind that that's where field theory is going. That's when I realized I had to catch up on the problem of gauge theory. I started doing it on a lattice because I figured that was the only way I could understand it. I did not want to have to sort through all the field theory literature on gauge theory. Of course at that point I have all the experience doing lattices from working with solid state, so that's the natural thing for me to do is to try to formulate the lattice version of the gauge theory. I did that, initially, just so I could have something that I was confident I could understand. Then I found myself faced with this problem that the lattice theory is something that has a simple strong coupling limit. It was the first experience in my life when I found that I could do the mathematics (the mathematics of solving the theory for strong coupling) but I couldn't figure out the physics. I just couldn't get any kind of concept in my mind as to what all the results meant when I did the strong coupling expansion. And I spent a full year just building a sense of the physics, working partly from the ideas of [Leonard] Susskind, partly [J.] Kogut-Susskind, partly just Susskind on strings, to build an ability to relate, to build a model physical world in which the strong coupling expansion made sense. That was a very different kind of experience from the experience that I had before, where the physics was not in question, it was a question of getting mathematical approximations to a known physics. But that's going off the subject that you're pursuing at this point.

PoS

But you do come back in the late 1970s to see whether renormalization group methods can be of help to quantum chemistry. What brings you back to that?

KGW

I had a graduate student named Ken Piech who did a very simple lattice model of atoms, and I studied it. I started thinking about it, and I realized you have different scales associated with the different electron shells. I started wondering what were the different energy scales associated with the different shells of an atom, and whether renormalization group methods would help you simplify that kind of problem. I started a program in quantum chemistry, and started with the presupposition that the renormalization group was going to make some big difference for quantum chemistry, and would bring in something new. Only I learned that the more I looked at it, the more impressed I was with the numerical methods that quantum chemists had already developed, especially with the use of expansions of wave functions in Gaussians. So most of the work I did was to try to build an analysis of why Gaussians gave you such good fits to all kinds of functions.

PoS

Do you see these developments -- what you had done in condensed matter physics, renormalization group, the parallel kinds of developments in quantum field theory, effective field theories and things like that -- as a paradigmatic kind of transition in terms of how physicists look at the world?

KGW

Yes, in the sense that, when I entered physics in the 1960s, there was a clear picture that quantum field theory was the ultimate answer for the laws of physics. Once we knew the right quantum field theory, the problem of determining the laws of physics was over. I saw the paradigm change from the idea that, if we did the strong interactions, we had the answer. I found myself coming to the recognition you had to treat the quantum gravity scale seriously -- it was not just something we didn't have to worry about. Then in my mind, although the rest of the field has not made this transition, as far as I can tell, realizing that you have no basis for assuming that the quantum gravity scale was necessarily the ultimate smallest scale either. A lot of people are going around saying, "if you solve quantum gravity, then everything is done." You know, like [Steven] Weinberg's Dreams of a final theory. But I don't know of anybody who is prepared to defend the proposition, even though the Greeks talked about it, that there is no smallest scale. Actually, I shouldn't say nobody. Feynman gave a talk at MIT on the next thousand years, and he was quite open to ideas such as further scales arising that are smaller than the gravity scale. I don't remember that he said it in so many words, but it was clearly in the spirit of his speech that the search for fundamental laws could go on indefinitely, with more and more ever smaller scales coming in. But that's not a popular idea among the people doing quantum gravity, as far as I can tell.

PoS

You once indicated that at a workshop it would be interesting for other people to exhibit their presuppositions and how they got transformed. Presumably it's part of our job to try to figure out how the collective presuppositions changed.

KGW

What you also want to look at, in that period before 1970, is how a field comes to grips with a very hard problem. One of the questions that is very interesting to me is to watch the period of time over which one person could work without a lot of help. You read about Kepler going for twenty years with essentially no encouragement or assistance of any kind. What I do remember is one conversation with Feynman. I wasn't the only one there, but somebody asked him, what did he find made physicists really exceptional? He said the thing that he noticed was that there was always persistence. But what I realized, in looking back on the period in the 1960s, was that what was really important about that period is that I was able to work by myself -- with some interaction, but not a whole lot -- and not just get lost, instead to have something useful come out the other end. Yet there is clearly a very long progression of internal changes in beliefs in the history of physics. Unfortunately I don't have a diary that would show you each time something happened that changed my internal beliefs about the problem I was working on, but I remember that the process became very clear, that I would get into a period when I would be very nervous and edgy and irritable, and that would go on for a while, and then an idea would come through and I would get very happy. I regret that I don't have a diary, so that you could have some description of each of the changes that took place along the way, because that's the kind of thing you would like to document: How long could a person keep going in the face of change after change after change? Obviously this was not a twenty-year process for me -- it went from 1963 to 1971 which was eight years. The most amazing developments, to me, are the people who have been able to stick with something for twenty years, and then come out with something at the end of it. When they succeed, it can be pretty extraordinary.

PoS

The economic conditions have changed, and it's not clear that very many people can afford to do that, right? You made a point earlier about getting tenure with only two publications.

KGW

The U.S. had a period in the 1960s when it was a buyer's market for positions in academe, and so a lot of people had this kind of opportunity. But at the same time, you look at how people struggled at the time of Kepler, at the kind of struggles he went through in order to be able to continue for twenty years, and it's clear there are many more people who, if they're willing to engage in the kind of struggle that Kepler did, can do it and not starve. A lot of people complain today that the conditions are tight, you have to toe the line and everything, but the people who are like Kepler are going just as stubborn today as Kepler was, as far as I can see.

PoS

What would you find useful and interesting in clarifying the entire history of this development, both in terms of communities coming together, and people like you straddling two communities? To some extent Kadanoff does the same, in contrast to Fisher or Widom, who were much more associated with a given community. What makes for innovation?

KGW

I would certainly like to see a description of the stages that Kadanoff and Wegner went through: How far they had gotten before they knew about my 1971 work, and what they needed, if anything, from that work, given everything they had done up to that time.

I think it is exceedingly important to understand how much they had already done. Often it happens that things develop, but no particular person really paying attention, like my going along for a long time without paying any attention to gauge theory. Suddenly I have to learn about it, I learn about it, and I proceed. It would be good to understand that, to have a description of the extent to which that was the way they worked too. In that sense Kadanoff and Wegner are far more interesting to me than anybody else as far as the development of the renormalization group applied to critical phenomena is concerned. The things I admire about Migdal and Polyakov have more to do with field theory than the critical phenomena.

PoS

How would you assess the contribution of the collective in this account? I seem to hear an accent on individuals: Kadanoff, Wegner...

KGW

There's a collective that's building around the concept of what they called scaling, which were the relations among the exponents, the self-similarity of the equation of state. That is clearly a collective effort, and of course closely tied to the developments in the experiments at that time and the link with the Domb work and so forth. That has become a collective phenomenon at that time, but I don't have any particular questions about that, because my questions about a collective all have to do with what happens after 1972.

PoS

Which is a different story.

KGW

To me there are collective things developing, but that doesn't fit to either extreme. From my perspective, I'm interested in the two extremes, of individuals struggling with a very hard problem, and the thing that I'm more interested in than anything else is identifying circumstances where you can't get from A to B because you need an individual, and no individual can do it. If I compare to the situation I'm dealing with now in the social sciences, the interesting question is, when did the pressure develop to go from A to B, and then how long did it take before it was possible to get from A to B? From that point of view, as you look at the collective working on the critical exponents, it raises the question, at what point did it become a question to try to understand the problem of non-classical exponents? You look at my work and you want to ask, what were the preconditions that made my work possible? What made it impossible (if it was indeed impossible) for somebody to do it five years earlier?

PoS

Right. You greatly clarify what it is that you bring, in terms of intellectual tools that allow you to go from A to B.

KGW

Right, and I can't imagine doing this without having the background of Gell-Mann-Low. To have something to start from.