Wilczek on the Problems of Fundamental Physics

Sean Carroll has a new interview up with Frank Wilczek in which they discuss, among other things, the problematic current state of fundamental physics. On the topic of string theory, here’s the discussion:

0:58:34.8 SC: Well, some of this worry has come out of string theory, many of our colleagues for the last several decades have pointed to string theory as the most promising way forward. As far as I know, you have not done a lot of work directly on conventional string theory. What is your feeling about that approach to moving beyond quantum field theory?

0:58:54.8 FW: Well, I think it has produced a lot of attractive work that’s intellectually rich and has spun off into fertile mathematics, but I don’t see that it’s been converging towards informative assertions about the physical world…

0:59:18.7 SC: That’s very elegantly stated, actually, yes.

0:59:21.0 FW: That you can check. And for me personally, I’ve kind of voted with my feet, I think there are more promising things to think about, that’s partially a sociological statement, but I think it’s, string theory is getting plenty of attention, it doesn’t need me. I’m happier doing things that other people aren’t doing, but that’s a personal statement, and so far, I haven’t regretted my choice, but I watch what people… I watch the subject and I watch what people are doing and I wish them good luck, and if and when things that I think are promising insights into the physical world emerge, I will pay a lot of attention.

1:00:12.3 SC: Sure Do you think that the rest of the field has voted with their feet in a slightly too uniform way, do you think that too much of our intellectual effort is going in that particular direction?

1:00:21.8 FW: I do, but I might be wrong, so I don’t want to discourage. Plenty of people are doing other things, so it’s not as if the rest of the world is feeling the lack of input from people who are working on string theory, it’s fine, people can work on string theory and it doesn’t hurt anything. I feel… Well, it’s going to sound, I don’t want to be patronizing, the people who do it are mostly adults and they know what they’re doing, but students and people who are thinking about what they’re going to do should go into it with open eyes. They should realize that the prospect of making an impact in our understanding of empirical science or technology are not… The prospect that you’ll make impact like that is probably not optimized by going into string theory.

1:01:20.8 SC: Yeah, no, actually, I think that we’re in exact alignment here. I feel a need to defend the string theory against unfair criticisms, but I do worry a little bit about the fact that it seems hard these days to connect it directly to empirical reality.

1:01:36.2 FW: Yeah, well, some nice ideas are coming off, as coming out as spin-offs, very, very clever people do string theory and they do clever things. So as I said, there’s been a lot of fruitful mathematics, there have been new techniques that have proved somewhat useful in condensed matter, although certainly not proportional to the amount of effort that’s going into it, and the future may look different, they may be real breakthroughs that come out of string theory that wouldn’t have come otherwise. But so far, the amount, I would say, other people may disagree, and I might be very unpopular among some of my colleagues for saying this, but I think the output compared to the input has been pretty disappointing on the empirical side.

I find it kind of remarkable that Carroll, known for defending string theory and string theorists, here reacts to Wilczek’s pretty negative characterization of string theory with “I think that we’re in exact alignment here.”

About current hot topic work on the black hole information paradox:

1:02:33.5 SC: Right. You have been involved in productive ways on the black hole information problem, which a lot of string theorists care about… What is your current feeling on the state of that problem? Do you think we’re making real progress?

1:02:50.8 FW: I think progress is being made in the sense that more intellectually coherent pictures are being drawn and some surprising connections to error correction and really interesting new chapters of quantum theory are emerging. On the other hand, it is a very esoteric problem, nobody’s going to produce… I don’t see a way, but who knows, but nobody has produced an experimental system to which these ideas apply in any reasonably direct way. So what does it mean to solve a problem like that? I’m not even sure what it means, where you can’t check. Many hypotheses go into it, the distance between the models and actual black holes that were phenomena you can observe are vast and many things could go wrong along the way in making these models.

1:04:04.7 FW: So I guess, yeah, it’s wonderful that people are making progress at the field, they’re making progress and have a literature that they enjoy, and it really is interesting from any point of view, it’s good, and maybe I should leave it at that, but how should I say? I don’t think it’s… I don’t think it’s the pinnacle of physics, let me put it… Let me put it that way.

On SUSY, Wilczek acknowledges

I’m a supersymmetry diehard.

which he certainly is.

If you look back at his many talks about prospects for the future, you’ll see that pre-LHC he was arguing

By ascending a tower of speculation, involving now both extended gauge symmetry and extended space-time symmetry, we seem to break though the clouds, into clarity and breathtaking vision. Is it an illusion, or reality? This question creates a most exciting situation for the Large Hadron Collider(LHC), due to begin operating at CERN in 2007, for this great accelerator will achieve the energies necessary to access the new world of of heavy particles,if it exists.

In the current interview and elsewhere, Wilczek makes clear the reason he believes in SUSY is his 1981 calculation with Dimopoulos/Raby showing that in SUSY versions of GUTs you could get the coupling constant evolution to overlap at the same energy. He’s still quite devoted to this argument, for him it’s of greater significance than the usual hierarchy problem arguments.

He has by now lost multiple bets that the LHC would see SUSY particles, including ones with Garrett Lisi in 2009 and Tord Ekelöf in 2012. At this point, even diehards like Wilczek acknowledge that chances that the LHC will see SUSY are slim. Another problem is that increasingly sensitive proton decay experiments have also ruled out a large part of the proton lifetimes predicted by the SUSY models Wilczek favors. He puts his faith in further proton decay experiments and a new, expensive collider. This is pretty much exactly the sort of thing that causes Sabine Hossenfelder to go ballistic over arguments for a new collider.

For a flavor of the SUSY discussion, here’s one piece of it, with Carroll starting off with a quite peculiar argument for SUSY:

0:29:28.8 SC: Yeah, maybe you can opine on this, but the way that I like to say it is, we could, in the space of all possible worlds that we live in, only one of them, we could have found supersymmetry already at the LHC very easily, but the fact that we haven’t doesn’t mean it’s not there. Maybe it’s less likely that it’s there, but it’s easy also to imagine theories where supersymmetry is real, and we just haven’t seen it yet.

0:29:53.1 FW: Right. So supersymmetry, as I said, there have to be… For supersymmetry to be valid, there have to be these superpartner particles that are the particles that the particles we know about turn into when they move into the quantum dimensions, but we don’t know what their masses are. We know some of their properties, but not their masses, and they could be very heavy. If they’re very, very heavy, we lose the benefit of improving… The benefit that supersymmetry would otherwise give in improving how the couplings unify, but okay, maybe that was a cruel joke on the part of nature. I want to think not, but the alternative is that they’re just a little bit too heavy to have been produced easily and identified easily at the LHC, and we just have to work a little bit harder and spend a little more money on…

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10 Responses to Wilczek on the Problems of Fundamental Physics

  1. paddy says:

    At the risk of being too facetious, it would appear that your problem is that your criticisms were both too early and not “very elegantly stated”.

  2. Peter Woit says:

    I do think that the consensus will likely be that I was a premature anti-string theorist who did not understand the proper way to explain to authority figures that they were wrong.

  3. André says:

    “Il est dangereux d’avoir raison dans des choses où des hommes accrédités ont tort.” Voltaire

  4. Scientists with secure positions tend to overestimate how much of a choice the vast majority of researchers in the field really have. Voting with our feet means, for most of us, leaving academia because we can’t pay rent from doing the research we think is promising. I have seen dozens of friends drop out that way, not because they wouldn’t have been able to get funding, but because they felt that the research they could have gotten funding/a job for would have been a waste of their time. The result is though, that some research just doesn’t get done, and academia remains a universe of research bubbles in which popular areas continue to float forever, carried by social reinforcement.

    I think it would be good if instead of listening to the top 0.1% of lucky scientists and their rosy experiences with academia over and over again, the media and podcast hosts and so on would spend some more time talking to the other 99.9% and ask them just why they work on what they work on. Better still, talk to some of those who left and ask them why. That should be eye-opening.

  5. Alessandro Strumia says:

    Last time I heard a seminar by Wilczek was when LEP closed and CERN organised talks to discuss what was the lesson. At that time some data suggested supersymmetry at LHC, while other data pointed in the opposite direction. But the talk was stubbornly one-sided.

  6. David Brown says:

    According to Wilczek, string theory has “… produced a lot of attractive work that’s intellectually rich and has spun off into fertile mathematics …” Has supersymmetry generated any new mathematics that mathematicians find impressive?

  7. Peter Woit says:

    David Brown,
    Supersymmetry has led to a lot of new mathematics. For instance, Witten’s “Supersymmetry and Morse Theory” paper is the founding document of the whole field of topological quantum field theory, and the Seiberg-Witten work on N=2 supersymmetric Yang-Mills revolutionized the field of four-dimensional topology with the Seiberg-Witten equations. One could argue that these developments are even more significant than what has come out of string theory.

    The problem with this, as with the mathematical advances coming from string theory research, are that they are pretty much in a direction orthogonal to the direction of the the string or susy unification program. As an idea about fundamental physics, what is relevant is N=1 4d SUSY and issues of its spontaneous breaking, and this is the part of SUSY that seems to have relatively little deep mathematical signficance.

  8. Peter Woit says:

    Alessandro Strumia,
    I’m completely mystified by Wilczek’s diehard attitude about SUSY. On other topics he’s a model of cautious, careful reasoning. Besides his very early paper with Dimopoulos/Raby, SUSY is not something he devoted much of his career to, so he’s not someone like Ellis or Kane who have much of their career invested in the idea. In addition, making many public statements that the LHC would decide the SUSY issue, together with losing mutiple public bets, you would think would argue for a stance of “looks like I was probably wrong on that bit of speculation”, not the diehard “there’s still a chance I was right, let’s build a new collider to find out”.

  9. Low Math, Meekly Interacting says:

    Isn’t it simply due to a hardened bias in favor of observable unification, which SUSY purportedly provides in an especially neat and (to some beholders) beautiful way?

    Perhaps this is overly provocative, but an alternative, which your last post may hint at, is that it’s pretty much the SM all the way up to the Planck scale, right? Maybe dark matter is taken care of by a (directly unobservable) sterile neutrino, gravity is “asymptotically safe” or something, and…that’s it. Nothing really new or interesting happens until you reach unimaginably high energies, things are the way they are for reasons humans can never conceive of , much less probe, and there’s essentially nothing left for HEP theorists to do.

    Maybe that’s the mother-of-all-nightmare-scenarios, and accepting SUSY is wrong makes it that much more plausible. It’s unacceptable because it kills an entire field of investigation that once occupied the very pinnacle of human achievement, perhaps never to be duplicated again.

    My deeply pessimistic psychosocial take.

  10. Marco says:

    > Better still, talk to some of those who left and ask them why. That should be eye-opening.

    Sadly, academia thinks of people that are critical of academia and have left as disgruntled scientists that were not good enough to succeed and are thus bitter, and shrug off any criticism (valid or not) from such persons.

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