This is something I wrote back in June, for context see the next posting.

First of all, there’s the following, which is not strictly scientific, but very relevant to how one decides to evaluate progress in a subject.

- The Maldacena AdS/CFT paper is almost 25 years old and has nearly 18,000 citations. Trying to exploit ideas based on AdS/CFT has been the main goal of thousands of the best theorists in the world for decades. Questions like “what about getting this to work in the more physical case of dS?” are not new but very old and have been the subject of tens of thousands of person-years of unsuccessful effort. This doesn’t mean it can’t be done, I think it does mean that what’s needed are some quite different ideas, there’s little point in further banging away at ones that haven’t worked for this long, after this much effort.
- Some of the hype surrounding AdS/CFT has been outrageous. One example is the claim that AdS/CFT gives a good way to calculate things about heavy-ion physics. This is just not true, and the people saying things like this should know better. Seeing people do things like this make me question their arguments about whether other ideas work or not (or have good prospects for working).
- As time goes on, people start using “AdS/CFT” to mean a wider and wider array of things. It often now denotes very general and vague conjectures about duality relations between gauge theory and gravity systems, or holography, or entanglement. It becomes impossible at some point to have a coherent discussion about the subject since there is no well-defined thing to talk about.

Sticking to the specific meaning of a duality between a specific superstring theory on AdS_5 x S^5 and N=4 super Yang-Mills on the conformal boundary, back in 1997 there were two reasons to get excited about this:

- Reading the duality as telling you about gauge theory in terms of string theory, you could hope that the duality could be extended to non-supersymmetric Yang-Mills, providing the long-sought string dual to QCD, allowing reliable strong-coupling QCD calculations. After a few years post 1997, it started to become clear this wasn’t working, and why. N=4 SYM has zero beta-function and is conformally invariant, so the effective coupling and physics are the same at all scales. QCD has a running coupling constant, with weak-coupling and strong-coupling physics very different. AdS/CFT allows strong-coupling calculations on the gauge theory side using weakly-coupled strings, but this has the same problems that we’ve always had with QCD: there are ways to write down strong-coupling expansions, but no way to match those to weak coupling physics, no way to capture the way physics changes from strong to weak coupling.
By the way, I noticed the Simons Foundation has just announced a collaboration to study QCD and strings

Foundation Announces the Simons Collaboration on Confinement and QCD Strings

and this doesn’t even mention AdS/CFT. People have tried really, really hard over decades to use AdS/CFT to say something about QCD, with very limited results. - Reading the duality as telling you about strings and quantum gravity in terms of gauge theory, the hope is to understand quantum gravity this way. There are a bunch of problems with this:
There’s the gravity in AdS rather than dS problem that you mention. As noted above, back in 1997 it was reasonable to expect a useful extension to dS. After 25 years of failed efforts, if there is such a thing it has to be something very different.

You want gravity in 4d, not 5d. This may not be a serious issue since you can take 5d with one small dimension, or brane or whatever to get rid of a dimension.

There’s a fundamental problem with doing gravity this way: string theory-based quantum gravity uses weakly coupled strings with the graviton a weakly-coupled mode. But this theory is dual to strongly-coupled gauge theory where you can’t calculate anything. So, AdS/CFT is telling you nothing about the usual picture of how gravity arises from string theory. What it supposedly tells you about are strongly coupled strings (using weakly coupled gauge theory), but then the connection to gravity is something very different than what was originally advertised for string theory.

Put together, the problem is that, to the extent AdS/CFT is telling you something about strings and quantum gravity, it’s telling you about the wrong kind of space-time (AdS) in the wrong dimension (5) with the wrong kind of strings (strongly-coupled). The general philosophy seems to be that at least it’s telling us about some kind of quantum gravity, which is a reasonable motivation, but leaves one far from real physics, in the land of general issues like resolving the black hole information paradox. But 20 years ago we were being told that it was resolved by AdS/CFT, then ten years later we were being told it wasn’t (the “Firewall”). Again, given the level of hype people operate with, it’s hard to evaluate any of this kind of thing with no relation to anything measurable.

I’m all in favor of good toy models, and from what I can see the main activity in AdS/CFT these days is trying to understand lower dimensional toy models. This leads to lots of interesting things to study, but you seem to end up with very complicated things happening even in much lower dimensions (0+1 SYK models, 1+1 JT gravity models), far from the 3+1 dimensions one wants. There are no physical gravity degrees of freedom below 3+1 dimensions, so it’s all too possible that what one is studying in these lower dimensional models is exactly the things of no physical relevance to the real problem.

Finally, my feeling has always been that the difficulty of measuring purely quantum gravitational effects means that the only convincing quantum gravity will be one unified with the rest of physics, fitting together well with what we can observe. The danger with studying pure quantum gravity is that you’ll end up with not one theory, but an infinite number of them, empty of any predictive value. The landscape is a realization of that danger.

**Update**: By the way, this is roughly the 25th anniversary of AdS/CFT, Scientific American has a piece by Anil Ananthaswamy.

The very first prediction of a property of the QGP based on AdS/CFT correspondence, $\eta/s=1/(4\pi)\simeq 0.08$, remains very close to the most accurate determinations from RHIC data. For example, Bass et al. (https://inspirehep.net/literature/1763462) find $\eta/s=(0.085\pm 0.025)$ at the critical temperature. Obviously, this prediction ignores all the differences between the two theories, such as finite $N_c$, finite coupling, different matter content. I’m happy to admit that it must be somewhat of a coincidence — but a remarkable coincidence it is.

It seems to me that quite a few of your arguments boil down to “There hasn’t been progress on X in 25+ years”

Using algebraic geometry as an analogy the motivic picture has developed tremendously since the 1960’s but the fundamental pieces of the program rest on existence theorems for algebraic cycles which no one knows how to prove. These are so out of reach that I wouldn’t be surprised if we saw no progress on even the weakest existence theorems this century.

Yet, this is a crucial issue and vast swathes of mathematics from the Langlands program to transcendental number theory are waiting to be revolutionized.

Going back to physics, imagine if in 2080 physicists finally manage to quantize string theories with Ramond-Ramond fields thus enabling computations beyond the supergravity limit in AdS/CFT.

Maybe in 2200 the QCD string is found and in 2500 M-theory is finally understood. The point being I don’t think the amount of time there hasn’t been progress means anything. So what if it takes a 1000 years?

Joseph,

The problem with AdS/CFT, as a way to do calculations in QCD, or as a theory of quantum gravity, is not that there has been no positive progress, but that all the work on it over 25 years has just clarified the underlying reasons why it doesn’t work. In the comments posted here I was trying to explain those underlying reasons. The problem is not positive progress being so slow that we have to wait til 2080, but that the derivative is the wrong sign: progress is towards proving that there is no way anything like this can work, that you need to find something quite different.

In the math analogy, it’s as if almost every implication of the motivic picture didn’t work correctly, giving completely incorrect relations between cohomology groups, and that those working on this keep saying “we still believe in the picture, we just need to keep calculating and maybe someday someone will come up with the right idea that fixes everything not working”. This situation would be a strong argument for abandoning the motivic picture. Some people might want to continue to work on it, but such work should be in the context of admitting the original ideas didn’t work, not continuing to hype them uncritically.

” What it supposedly tells you about are strongly coupled strings (using weakly coupled gauge theory)”

Incorrect.

Gauge theories at large N are dual to weakly coupled strings.

Weakly coupled gauge theories are dual to tensionless weakly coupled strings.

Indeed, strongly coupled gauge theories at large N are dual to ‘standard’ gravity, but such gauge theories are under much better control analytically/numerically when compared to gravity. Also, we ‘know’ their completion to finite N and any coupling using the same techniques.

Anonymous,

You’re taking the quote out of context, also out of the context of what this email was about. The point I was making is that AdS/CFT is completely irrelevant in the usual picture of how string theory is sold as the answer to quantum gravity: gravity as the effective space-time low energy theory due to the graviton mode of a weakly coupled string. In this picture you can compute how the strings behave using perturbation theory, AdS/CFT is irrelevant.