Blogging has been light recently, partly due to quite a bit of traveling. This included a brief trip the week before last to Los Angeles, where I met up with, among others, Sabine Hossenfelder. This past week I was in Washington DC for a few days, and gave a talk at the US Naval Observatory, one rather similar to my talk earlier this year in Rochester. In addition, I’ve been trying to spend my time on more fruitful activities, especially a long-standing unfinished project to make sense of the relationship between BRST and Dirac cohomology. Optimistically, I’ll have a finished (or at least finished enough to make public) version of something later in January, after taking a couple weeks at the beginning of the month for a vacation in France.

I’m completely in agreement with Sabine about the sad state of high energy particle theory, and glad to see that she has been forcefully trying to get people to acknowledge the problem. I don’t agree though with her “Lost in Math” characterization of the problem, and my talks in DC and Rochester tried to make the case that what is needed is more interaction with mathematics, not less.

Various things that might be of interest that have to do with the state of high energy physics theory are the following:

- A Y Combinator blog interview with Lenny Susskind. I think it’s fair to say that Susskind now admits that string theory, as currently understood, cannot explain the Standard Model, and that as a result he has given up on trying to make any progress on particle theory. He says:

My guess is, the theory of the real world may have things to do with string theory but it’s not string theory in it’s formal, rigorous, mathematical sense. We know that the formal, by formal I mean mathematically, rigorous structure that string theory became. It became a mathematical structure of great rigor and consistency that it, in itself, as it is, cannot describe the real world of particles. It has to be modified, it has to be generalized, it has to be put in a slightly bigger context. The exact thing, which I call string theory, which is this mathematical structure, is not going to be able to, by itself, describe particles…

We made great progress in understanding elementary particles for a long time, and it was always progressed, though, in hand-in-hand with experimental developments, big accelerators and so forth. We seem to have run out of new experimental data, even though there was a big experimental project, the LHC at CERN, whatever that is? A great big machine that produces particles and collides them. I don’t want to use the word disappointingly, well, I will anyway, disappointingly, it simply didn’t give any new information. Particle physics has run into, what I suspect is a temporary brick wall, it’s been, basically since the early 1980s, that it hasn’t changed. I don’t see at the present time, for me, much profit in pursuing it.

- Susskind instead spends his time on highly speculative ideas relating geometry and quantum theory, with the idea that while this has no connection to particle physics, it might somehow lead to progress in understanding quantum gravity. Natalie Wolchover at Quanta has a new story about Susskind’s latest speculations.
- This past week the Simons Foundation-funded “It from Qubit” collaboration has been having a two-part conference. This started at the IAS, talks available here, then moved on to the Simons Foundation headquarters in NYC (see here). Videos of the IAS part are available, for the NYC part, there’s Twitter. George Musser reports that Juan Maldacena has figured out how to construct (in principle) traversable wormholes, and that he’s arguing that “quantum computers are so powerful that they create spacetime”. For a tweet showing a summary of what has been achieved, see here.
Personally I’ve always been dubious that we’ll ever have a useful “quantum theory of gravity” unless we have some sort of unification with the standard model, which would provide a connection to things we can understand and measure. Lacking such a connection, another way to go would be to try and evaluate a “quantum theory of gravity” proposal based on its mathematical consistency, coherence and beauty. My problem with the “It from Qubit” program is that, ignoring the way it gives up on connecting to what we understand, I’ve never seen anything coming out of it that looks like an actual well-defined theory of quantum gravity that one could evaluate as a mathematical model consistent with quantum mechanics and what we know about 3+1d general relativity.

- For something about quantum computation and its relation to fundamental physics that I can understand, John Preskill has a wonderful article on Simulating quantum field theory with a quantum computer. Nothing there I can see about quantum gravity.
- Given that its founder Susskind and the other leading figures of the field at the IAS have pretty much given up on the project of relating string theory to particle physics, an interesting question is that of why the pathology of so many researchers still working on this failed project? The source of this pathology and the question of what can be done about it I think are at the center of Sabine Hossenfelder’s book and recent blogging. An important question that is getting raised here is that of the damage this situation is doing to the credibility of science. If you want to fight the good fight against those who, because it threatens their tribe, want to deny the facts of climate science, is it helpful if many of the best and brightest in science are denying facts that threaten their tribe? Scientific American has a story about Why Smart People Are Vulnerable to Putting Tribe Before Truth, but it doesn’t make clear the depth of the problem (i.e. that some of the smartest scientists around are doing this).
- For an example of the problem, see an interview with Gabriele Veneziano about the history and current state of string theory. He’s in denial of the obvious fact that string theory makes no predictions:

People say that string theory doesn’t make predictions, but that’s simply not true. It predicts the dimensionality of space, which is the only theory so far to do so, and it also predicts, at tree level (the lowest level of approximation for a quantum-relativistic theory), a whole lot of massless scalars that threaten the equivalence principle (the universality of free-fall), which is by now very well tested. If we could trust this tree-level prediction, string theory would be already falsified. But the same would be true of QCD, since at tree level it implies the existence of free quarks. In other words: the new string theory, just like the old one, can be falsified by large-distance experiments provided we can trust the level of approximation at which it is solved. On the other hand, in order to test string theory at short distance, the best way is through cosmology. Around (i.e. at, before, or soon after) the Big Bang, string theory may have left its imprint on the early universe and its subsequent expansion can bring those to macroscopic scales today.

This take on how you evaluate a theory by comparing it to experiment is not one that will give the average person much understanding of the scientific method or much confidence in scientists and their devotion to it.

> I don’t agree though with her “Lost in Math” characterization of the problem,

> and my talks in DC and Rochester tried to make the case that what is needed is

>more interaction with mathematics, not less.

In fact Sabine says essentially the same thing in her blog and her book; this is probably not well reflected in the book’s title, though.

Peter,

I am certainly not saying that physicists need less contact with math (or less math, period). I am saying they need to be more careful using their math. Look at the issue with naturalness I go on about in the book – this would have been preventable had physicists actually bothered to write down their assumptions and made derivations from that. Indeed, my major conclusion in the book is that physicists should focus on mathematically well-defined problems. (Lack of naturalness is not one of those – at least not in the present formulation. Maybe it can be made into on. I tried but did not succeed at that.)

This is why I am not a fan of unification attempts – it seems mathematically unnecessary to me. This is not to say that one should not work on it, just that because of the lack o a well-defined problem, it’s likely to end up in guess-work and beauty-arguments that result in useless theories.

I also note, however, that mathematics *alone* will never be sufficient, in case that’s what you are referring to.

It’s right, in a sense, that string theory does make predictions. It predicts, erm, strings. It’s just that you’d reliably see those (say, in terms of excitations) only at ridiculously high energies. You know that story, so I’ll not repeat it.

Also, as I tried to explain in LA, it seems to me entirely possible to test the weak-field approximation. I wrote about the (type of) experiment I had in mind here. As I pointed out, it would be good if someone bothered making predictions for that. Composite objects in quantum superpositions of position eigenstates. I don’t understand why no one even seems to care.

Srsly, Peter, think about this for a moment. You sit in a room with a group of people who have spent big parts of their life thinking about how to improve our understanding of the fundamental laws of nature, and no one has ever even heard of the one experiment that’s possibly about to just test it? Witness the confusion in the room. How come? What the heck is going on in this community? Can you see why I keep going on about how bad we are in aggregating information and how big of a problem that has become?

I wish use of the time ball were not merely an annual ceremonial event these days.

Sabine,

My sense was that your title “Lost in Math” was really referring to the practice of dressing up purely subjective and biased human judgments to look like rigorous and sophisticated mathematical arguments, to the point where the subjective basis of certain ideas becomes very obscure. So it wasn’t meant to be critical of using mathematics per se. Is that a fair summary?

Sabine,

I think where we disagree is that I do think that the pursuit of unification attempts is worthwhile, even if not “mathematically necessary”, and that, absent new experimental data, such work is going to need to rely on judgments which can be characterized as judgments of “beauty”. The problem is that a lot more clarity and honesty is needed in evaluating “beauty”. Right now for example, we have string theorists arguing for the “beauty” of string unification, without acknowledging that all known ways of getting this unification are actually hideously ugly (realistic string vacua).

To get away from ill-defined terms, maybe a better way of saying things is that I see the history of fundamental physics as involving a sequence of deeper understandings of the implications of symmetry, and I think we should be looking for the next, deeper, way of understanding such implications. For a specific example, our current understanding of gauge theory invokes BRST symmetry, which may very well need to be replaced by a different, more powerful (and more beautiful…) mathematical structure. I would agree that what people are mostly doing, endless repetition of attempts to get something out of the same old symmetry arguments, is getting “lost in math” and goes nowhere.

About string theory predictions, the problem is you need to say what you mean by “string theory”. It’s interesting that Susskind is well aware of the problem and tries to explain it: the “string theory” we understand, perturbative string theory, can’t give a consistent model that looks like the real world. Guesses as to what the true consistent version of string theory is supposed to be don’t necessarily involve strings at high energy (e.g. you may instead see some sort of M-theory background with no strings).

About the problems with purely quantum gravity research, I think we agree. I am less optimistic though about such research, in the absence of any new ideas about the relation of internal and space-time symmetries that would connect such research to what we can understand and measure about particle physics.

Gabriele Veneziano says that string theory “predicts the dimensionality of space.”

Correct me if I’m wrong, but doesn’t it predict 10 dimensions? You can compactify it to 4 dimensions, but is there any good reason to prefer 4 dimensions over 5, 6, 7, 8, 9, or 10? If there isn’t, I am not very impressed by this prediction.

You’re kind to Leonard Susskind: I recall how rude and dismissive he was towards you back in the day. I always found it hard to reconcile this with the genial figure he appears to be in his (excellent) many video lecture series; many of which are community outreach.

Ted,

Yes, that’s a good summary.

Peter,

I don’t think there’s anything to learn from debating in which sense string theory or unification is beautiful or not. Look at what has historically worked: It was either developments guided by experiment (say, electrodynamics), or it was an actual mathematical inconsistency (special relativity, Dirac’s equation, renormalizability of the weak interaction).

The conclusion I draw is that we’d be well-advised to stop talking about beauty and focus on these two types of problems: inconsistency with data, and internal inconsistency. Everything else is just poking in the dark. May work, but it’s unlikely to work.

Veneziano was probably referring to calculations he’s done himself on graviton scattering and the like, see eg 1008.4773 and similar.

Peter Shor,

Yes. Together with his explanation that string theory predicts unseen long-range forces, Veneziano’s argument seems to be that string theory does too make predictions, wrong ones. Bizarre.

Peter Donnelly,

For context to your remark, there’s an old blog posting about this:

https://www.math.columbia.edu/~woit/wordpress/?p=454

Also for context, one of the blurbs on the back of the French edition of Susskind’s QM book is from me.

I’ve never really met Susskind (I did once ask him a hostile question at the end of a colloquium talk…) and, to the extent there are examples of rude and dismissive comments from him about me, I never taken them personally. He’s not the only well-known string theorist I’ve never met who is generally known for their good humor and generous behavior, but seem to lose it when dealing with a challenge to a research program they are heavily invested in.

I must speak out in support of Sabine Hossenfelder’s point of view. To me, most of the talk about ‘beauty’ in mathematics (and theoretical physics) smacks of over-romanticization.

For one thing, the experience of ‘conceptual beauty’ is somewhat dependent on one’s skill-level. By the time one understands a concept sufficiently thoroughly that it becomes trivial, the concept has lost most of its beauty. There is an experience of beauty in the ineffable sense that not everything is fully comprehended or accounted for. Furthermore, I don’t want to go so far as to say that “beauty in mathematics is subjective,” e.g. because there are legion mathematical concepts and theorems that many people do agree about are beautiful, but of course it goes without saying that it is subjective enough that it would complicate discussions endlessly if it were taken as a criterion for scientific progress.

But I would like to go further. I see the following problem with an over-emphasis on beauty as a criterion for truth — rather than say, regarding beauty as being a by-product of truth, which to me seems to have the virtue of not unnecessarily obscuring matters. The problem is that it endows science with a special kind of mystique, since it adds a further quality to the list of necessary requirements for the prospective scientist: this person must be able to feel and appreciate the

beautyof science. We risk turning the scientist into a kind of 21st century priest, a person with a mysterious insight into a non-empirical matter such as ‘mathematical beauty’.I think we have definitely advanced a long way along this road, of turning science into a new kind of religion. And the current malaise in high-energy physics, with its curious blend of mathematical fetishizing and crazy unfalfisiable sci-fi thought experiments (Are there parallel universes?? Are we living in a simulation??), to me is the best kind of proof of this.

So the best thing we can do is voice a clear

noto everything that is bad about non-scientific thought. Perhaps we should even get clear first about what has brought science so far to begin with, because so many people seem to regress into unscientific and irrational modes of thinking precisely under the guise of scientific thought. If we do not want to get completely lost in a pseudo-scientific fantasy world, I think we should start soon.Erstwhile number-theorist,

I think Sabine in her comment does a good job of making precise the “don’t pay attention to beauty” argument. The argument is that in physics one has made progress by paying attention to inconsistency, either internal or with data, that anything else is “poking in the dark” and unlikely to work.

My counter-argument is that, on many questions about fundamental physics, the field is facing a lack of experimental inconsistencies, and not very good prospects for finding new ones anytime soon. I agree that under the circumstances, focus should be on internal inconsistencies, and there is far too little of that. But, in this situation, with guidance purely from the formal structure of the theory, one is in much the same situation that mathematicians have always been in. And, in mathematics, I’d argue that only paying attention to logical consistency isn’t enough: if that’s all you demand, you’ll end up with a large amount of consistent but empty knowledge. For example, you may very well find lots of complicated, but consistent, ways of reconciling quantum theory and gravity. If you end up with an absurdly complex untestable mess like the string landscape, the fact that it may be logically consistent is not enough to make it a promising path forward.

Something more than consistency is typically involved in inspiring great new mathematical ideas, with a “search for beauty” one ill-defined way to characterize what sometimes motivates the research from which some such ideas emerge. Yes, this is a very hard way to make progress on fundamental physics, but it is not impossible to find new ideas and make progress this way, and it may be the only choice people have who want to continue to work on certain questions. Some people should be pursuing this, and to have any success they’ll have to have something a lot more sophisticated than a naive idea about what is beautiful and what isn’t beautiful. I’d argue that the best mathematicians often are motivated by such ideas.

I agree with much of Sabine’s argument, but I have a somewhat different perspective on one aspect of it, which is her criticism of the concept of naturalness, which is the requirement that any pure dimensionless constants in the parameters of a physical theory that are not order unity require explanation. We say a dimensionless constant that is orders of magnitude away from unity requires “fine tuning.” The standard model has, depending on what you count, 29 dimensionless parameters, most of whom are not order unity and hence are fine tuned. The lesson that many people took away from this fact was to attempt to embed the standard model in another, possibly more unified theory, with fewer adjustable finely tuned parameters. Examples that were proposed included technicolour and supersymmetry. These failed, in some cases in more than one way: for example, the minimal supersymmetric extension of the standard model has more parameters-not fewer, and indeed 105 of them, which is not a small problem. And they are not less fine tuned than the original parameters.

This was not an aesthetic imperative, for we do not seek to reduce the number of finely tuned parameters to make a theory more beautiful, but to increase its explanatory power. This is a general aim of science.

What I take away from the failure of these attempts is that we have to accept on face value that the parameters of the standard model have been fine tuned to unnatural values. This requires explanation. One form that such an explanation could take would be if sometime in the past there acted a physical mechanism which choose such unlikely values for the parameters.

I have suggested one possible mechanism for this fine tuning, which is cosmological natural selection. This is falsifiable and hence will probably be shown wrong. But that is the price you pay for a genuine increase in the explanatory power-if true-of the hypothesis.

My bottom line, then, is that when taken to describe a physical theory, beauty is sometimes a measure of explanatory power, and this can be a good thing. Of course it often is not, in which case Sabine’s arguments apply.

Thanks,

Lee

@Lee:

When you say that “any pure dimensionless constants in the parameters of a physical theory that are not order unity require explanation,” you are implicitly putting a probability distribution on the positive reals which is sharply peaked at unity.

Doesn’t this assumption also require explanation? Why should the range of numbers between 1 and 2 be any more probable than the range between 10^10 and 10^20? Aren’t there just as many numbers in the range between 10^10 and 10^20? as there are between 1 and 2? (Uncountably many in each.)

Thanks again for the links, I don’t know how you find all of these.

Susskind said something else which everyone on this blog seems to be ignoring. At about 14:47 he says “will what does correctly describe particles be a small modification of [string theory] or a big modification, that’s what I don’t know.”

Thus, if we are going by what Susskind says, we should start with string theory and modify it, not abandon it.

Dear Peter Shor,

Yes, exactly, and let me explain where that expectation for dimensionless ratios to be order unity comes from.

Part of the craft of a physicist is that a good test of whether you understand a physical phenomena-say a scattering experiment-is whether you can devise a rough model that, with a combination of dimensional analysis and order of magnitude reasoning, gets you an estimate to within a few orders of magnitude of the measured experimental value. People like Fermi and Feynman were masters at this, a skill that was widely praised and admired.

The presumption (rewarded in many, many cases) was that the difference between such rough estimates and the exact values (which were by definition dimensionless ratios) were expressed as integrals over angles and solid angles, coming from the geometry of the experiment, and these always gave you factors like 1/2pi or 4pi^2, which were order unity.

Conversely, if your best rough estimate does not get you within a few orders of magnitude of the measured value, then you don’t understand something basic about your experiment.

Seen from the viewpoint of this craft, if your best estimate for a quantity like the energy density of the vacuum is 120 orders of magnitude larger than the measured value, the lesson is that we don’t understand something very basic about physics.

Thanks,

Lee

@PeterShor

Gabriele Veneziano can be seen in a video entitled “Why Four Dimensions and the Standard Model Coupled to Gravity … “. The speaker explains (following Solid Theoretical Research In Natural Geometric Structures) how “dimension 4 appears as a critical dimension because finding a given manifold as an irreducible representation* requires finding two maps to the sphere such that their singular sets do not intersect. In dimension n the singular sets can have (as a virtue of complex analysis) dimension as low as n-2 (but no less) and thus a general position argument works if (n-2)+(n-2) is less than n, while n=4 is the critical value. ”

I let curious people to find out easily the source of this quote. To understand it is more challenging and requires some knowledge in differential geometry and operator algebra…

Another relevant detail I think for the issue discussed by Peter in his post: the speaker in the video is not Veneziano and is pretty well known to be doubtful about string theory. Nevertheless at the end of this video he praises publicly the italian theoretical physicist : “It’s crucial we have doubts and we manifest these doubts… if we are just preaching this is a catastrophy… I admire Gabriele for that … we spend our life doubting , the chance we are right are tiny”. The speaker and Veneziano had been professors at College de France at the same time for a while. Both are emeritus now.

PS: the link to the video is https://www.youtube.com/watch?v=qVqqftQ92kA

* irreducible representation of a specific operator algebraic equation…

quanta by any other name:

Your Susskind quote I think reflects one of the most serious problems facing this field of physics. For Susskind and many others, string theory has become such a dominant paradigm that, despite its complete failure as a unified theory, they cannot even envisage looking for a completely different starting point. The only conceivable direction for progress is to start with string theory and modify it, by a small or big amount. I think Susskind recognizes this hasn’t worked so far, but after spending decades devoted to this ideology, he can’t conceive of trying to start from a different point.

As someone who has been led by the nose to some problems of “quantum geometry” in low dimensions (through some possible applications to mundane topological condensed matter systems), I’ve been digging through the old string textbooks like GSW to extract useful technology.

The thing I’ve never understood, and still don’t understand, is why choose D = 26 for the bosonic string. The classical theory of the 2+0-D massless bosonic worldsheet decouples from the geometry of the sheet in the conformal gauge. The anomaly (if I understand correctly) says that the stress tensor acquires a nonzero trace whenever the worldsheet is not flat, proportional to the (gauge invariant) scalar curvature, unless we have 26 bosons to cancel the negative central charge of the Fadeev-Popov ghosts.

This just means that the free fixed point is unstable due to quantum corrections, right? The generation of a nonzero stress tensor trace from the scalar curvature looks like gauge invariant statement. If you want to study quantum strings (forget for the moment whether they have anything to do with gravity), then going to D = 26 makes that task easier, modulo the tachyon problem. But if you want a 3+1-D theory, can we be sure there isn’t some strong coupling fixed point which itself could be critical (conformally invariant), but not perturbatively connected to the free one? Are we really forced to go to the critical dimension by physics, or is it just mathematical convenience (essentially integrability of worldsheet CFT) in this case??

Matt Foster,

This is a rather off-topic technical question. There’s a huge literature on string theory in non-critical dimensions, and many people over the years have looked into this. I think a fair summary is that no-one knows how to get a realistic unified theory this way, thus the concentration of attention on starting with strings in the critical dimension then somehow getting rid of the excess dimensions.