Graham Farmelo’s new book The Universe Speaks in Numbers has recently been published in the UK, US publication is next week. The topic of the book is one close to my heart, the relationship of mathematics and physics. I’m very much in agreement with the main argument of the book, which is that our most fundamental theories about physics have turned out to naturally be expressed simply and beautifully in terms of deep ideas about mathematics. This surprising congruence between the deepest ideas in two seemingly different fields strongly indicates that they share an unexpected unity. As fundamental physics reaches technological limits on the experimental side, investigating the underlying mathematical structures may be the best and only route open to further progress.
Much of the book is historical (and often Anglo-centric), beginning with Newton, a figure who made huge tightly intertwined advances in both mathematics and physics. Looking at Newton’s career, it makes no sense to characterize him as a mathematician or a physicist, he’s both in equal measure and at the same time. Farmelo then moves on to Maxwell, who also revolutionized physics while at the same time introducing important new mathematics into the subject. He tells the story of Maxwell’s 1870 talk “On the relations of mathematics to physics”, then a couple chapters later it’s Dirac’s 1938 talk “The Relation between Mathematics and Physics”.
In Farmelo’s account:
Dirac quickly arrived at what was, in effect, a manifesto for research into theoretical physics. He proposed a new principle – the principle of mathematical beauty – which says that researchers should always strive to maximize the beauty of the mathematical structures that underpin their theories of the natural world…
He concluded that “big domains of pure mathematics will have to be brought in to deal with the advances in fundamental physics”…
Eventually the two subjects might possibly become unified, Dirac suggested, with “every branch of pure mathematics then having its physical applications, its importance in physics being proportional to its interest in mathematics.”
A major reason for Dirac taking this sort of view was the example of Einstein’s work on general relativity, which to reach fruition had required Einstein to become expert in the newly developed and rather challenging abstract mathematical machinery of Riemannian geometry. The two great pillars of modern physics, relativity and quantum theory, are deeply related to central modern ideas about mathematics, in particular, respectively, geometry and representation theory. While in the case of relativity the mathematics came first, for the case of quantum theory, the mathematics underlying the subject was mostly developed later.
Farmelo goes on to explain that relations between math and physics entered a fallow period during the 1950s and 1960s, but the advent of gauge theory and the Standard model led to a productive renewal of healthy relations during the 1970s. He does a good job of explaining how this came about, discussing in particular the central role played by Witten. Farmelo has benefited from getting to talk to Witten himself in some depth about this, and gives a nuanced portrayal of Witten’s rather complex and evolving feelings about the relations of the two subjects and the role that he and his immense talents have played in this story.
There’s a great deal of the usual sort about the history of string theory, emphasizing its points of contact with new mathematics. The next to last chapter is about Nima Arkani-Hamed and the amplituhedron story, portrayed as the latest exciting development on the math-physics front. Farmelo is clearly enthralled by Arkani-Hamed and his intense enthusiasms. The evolution of Arkani-Hamed from phenomenologist to mathematical physicist is definitely a fascinating thing to observe, and I’ve often written about it here (you might want to for instance read this posting). Farmelo also points to an excellent lecture by Greg Moore on Physical Mathematics and the Future (discussed here), which I think is based on a much deeper understanding of the current state of the math/physics relationship, and gives a much broader perspective than the narrow one of the amplituhedron. By the way, I see on Moore’s website that he’s writing up for the 2019 TASI school what appears to be an excellent set of notes about Chern-Simons theory and related topics.
A major problem though with this book is that it pretty much completely avoids the big problem raised by the program of pursuing progress in fundamental physics through beautiful mathematics: how do you know whether people doing this are on the right track or headed down a blind alley? Farmelo starts the book off with a very odd preliminary chapter comparing Einstein’s work at the IAS in his later years to that of his modern day successors:
[Einstein] was seeking a new theory, not in response to puzzling experimental discoveries, but as an intellectual exercise – using only his imagination, underpinned by mathematics. Although this approach was unpopular among his peers, he was pioneering a method similar to what some of his most distinguished successors are now using successfully at the frontiers of research.
The fact of the matter is that, in retrospect, Einstein’s work of this era was a huge failure, as he got stuck deep down a blind alley. He was seduced by a specific speculative idea about how to get unification out of mathematics, by using simple extensions of the differential geometry that he had such success with in the case of GR.
How does Farmelo know that string theory enthusiasts following Einstein haven’t run into the same problem he did? In essence, Farmelo just assures us that he has talked to them and they tell him that, like Einstein before them, they think they’re on the right track. The existence of skeptics is mentioned, but their writings are carefully excluded from the 200+ item bibliography. Jim Baggott, Sabine Hossenfelder and I (and our writings) appear only in a short footnote on page 6, with bloggers described as complaining that “modern physics should get back on the straight and narrow path of real science”. But the three of us are complaining about, not “modern physics”, but one small subset of it, and at least in my case, the path I argue for is almost exactly what Farmelo is arguing for: absent help from experiment, pursue the path advocated by Dirac.
Here’s part of Farmelo’s summation of the current situation in the book’s last chapter:
The great majority of today’s leading theoretical physicists are, however, confident that they are motoring steadily in the right vehicle, despite the problems they are having in trying to drive it.
In the public domain, the debate about the merits of the string framework has been raging for years, especially in print and online. Some of these onslaughts are useful correctives to the hype lavished on this programme and to the superciliousness of pronouncements made by some string (although rarely by the best ones in my experience). Experts on the string framework have every reason to be proud of the progress they have made, but until such time as experiments confirm its validity, there is no room for smugness. Yet I am often troubled by the dismissiveness of some of the critical commentators, especially those who write with a confidence that belies the evident slightness of their understanding of the subject they are attacking. Opposing the view taken by leading theoreticians might be interpreted as a healthy disrespect for orthodoxy. However it may be part of the worrisomely common view that anyone can have a valid opinion on any subject, regardless of their technical knowledge and appreciation of it. In scientific matter this trend is especially regrettable.
The first part of this I think is simply not true, with most “leading theoretical physicists” these days unsure what the right direction is for how to get beyond the Standard Model. As for the last bit, I’ll just say that I think it can accurately be described as “sleazy” (by the way, Farmelo at one point came to see me in New York when he was doing research for the book, and we had a quite pleasant conversation, he’s rather charming). Besides the ad hominem attack on unidentified critics, there’s nothing anywhere in the book about the actual problems of the vehicle some people are motoring in. For instance, the problem of the landscape and the multiverse is dealt with by just ignoring it, it’s not mentioned at all. If it had been mentioned, Farmelo might have had to deal with the fact that it’s mathematically hideous, so a direction which should be abandoned by his own arguments.
In the end, my feelings about this book are much the same as in the case of Farmelo’s biography of Dirac (see here): a wonderful book in many ways, but marred by a bizarre degree of string theory fanboyism. While there’s a lot to like about this book, and much of it makes a good case for a controversial point of view that I strongly agree with, unfortunately the problems with it are even more serious than in the case of the Dirac biography.
The IAS is having a public event next week, convening a panel to discuss the math-physics issues brought up by the book. I may add something here about this after it happens. Perhaps someone in attendance can get a show of hands from the assembled leading theorists to see if they really feel that they’re steadily motoring in the right vehicle or not.
Update: I’m listening to a live-streaming version of the IAS event here. After a talk by Farmelo, mainly about history, and a discussion with Karen Uhlenbeck and Freeman Dyson (moderated by Natalie Wolchover), Greg Moore is now giving a talk (available here) on TQFT and gauge theory which is quite good. I’m very much in sympathy with his take on “physical mathematics”.
Update: Besides an advertisement by Nima Arkani-Hamed and Thomas Lam for their work on amplitudes, the only discussion of the current state of the math/fundamental physics interface was the final short conversation between Dijkgraaf and Witten. Looking back at expectations from 30 years ago, Witten said he had expected progress on understanding the laws and principles behind string theory, but that has not occurred. Dijkgraaf tried to end with a defense of string theory as “well, by AdS/CFT it’s connected to QFT, so it somehow is connected to the real world”, to which Witten said something like “we shouldn’t give up hope for string theory as a unified theory, we might yet find the right string theory vacuum”. In the end Witten said that he found it hard to accept the possibility that the unexpected things discovered through string theory didn’t mean that it had to do with a unified theory, but admitted he didn’t have a scientific justification for this.
Update: There’s a review of the book by Tony Mann at Times Higher Education. It includes:
Farmelo’s book is a response to these contrarians [Hossenfelder and myself]. He is confident that the beauty of the mathematics is significant in indicating that we are on the right track, and that eventually, even if we have to wait for many years, we will be able to test string theory against new experimental evidence. As a spirited defence of the idea that beautiful mathematics should be a guide for physicists, Farmelo’s book is a timely response to critics such as Woit and Hossenfelder, defending what science writer Jim Baggott has called “fairy-tale physics”. Ultimately I am not sure, however, that he makes his case anything more than a matter of faith.
I think Mann gets it right that the Farmelo book is intended as a defense of string theory against the Baggott/Hossenfelder/Smolin/Woit critique (with the odd feature that he refuses to allow mention of our books in the bibliography, or to engage in any way with the arguments we make), and that his argument comes down to little more than “trust certain famous theorists”, especially those at the IAS. As usual, I’m inaccurately portrayed as opposed to the idea that progress can be made by following beautiful mathematics. The problem with string theory unification is that it’s a failed physical idea, with the failure indicated not just by lack of predictivity, but also by the fact that string theory models compatible with observations are horrendously ugly.
Update: The Dijkgraaf-Witten conversation is available here. Some extracts from near the end.
Witten: I’m actually personally reasonably confident that what we’re doing is a lasting contribution. But I’m less confident that we’ll really be able to put it on a completely solid footing. It depends on being lucky with experiment, I would say…
Dijkgraaf: Often I hear questions about whether is string theory wrong or right, but I often answer there’s no way in which we’ll ever get rid of string theory, because in some sense it’s an integral part of the theories that we already are using.
Witten: That’s true but not completely satisfying. Let’s not give up on the dream of finding the vacuum that describes the real world…
The honest answer is that personally as I told you before I have confidence that the general enterprise is on the right track, but I don’t claim that the argument I’ve given is scientifically convincing.
Witten makes clear that at this point he has no likely forseeable experimental results relevant to string theory he can point to, no “scientifically convincing” argument that it’s on the right track, just a feeling that since string theory research has turned up various points of contact with important math and physics, there must be something right about the idea.
Update: Siobhan Roberts at the New York Times has a piece about the centenary of the eclipse that made Einstein famous that also discusses Wednesday’s IAS event.
There is a lot of mathematics. Some of it beautiful, some of it not so much. Some of it describes our world, some of it does not. How do we find the math that describes our world?
That’s the relevant question that anyone should ask who is interested in progress in the foundations of physics.
Relying on beauty has not worked in the past and it’s not presently working, so clearly this is not what physicists should do.
Likewise, working on a theory just because a lot of other people work on a theory, is also not a good reason to think that this theory tells you something about the real world.
And without these two arguments, what is left of string theory? Not much. It’s not that it’s entirely uninteresting, of course. It’s just that the resources that have gone into it and continue to go into it vastly exceed the reasonable. And throwing further money at it just encourages people to produce more useless papers, like on the swampland and such. And don’t get me started on folks who seem to think we live in Anti de Sitter space.
Seriously, Peter, I ask you. How can anyone in their right mind still think that this has something to do with describing reality? Why are these people still receiving research grants?
S.H. said :
“How do we find the math that describes our world?
Here’s an interesting read, from Lee Smolin, on the subject, as he tracks Einstein’s modus operandi :
The introduction says :
” There is a myth that Einstein’s discovery of general relativity was due to his following beautiful mathematics to discover new insights about nature. I argue that this is an incorrect reading of the history and that what Einstein did was to follow physical insights which arose from asking that the story we tell of how nature works be coherent. “
Dear Peter, I read that the commenter Sabine Hossenfelder has written
”And don’t get me started on folks who seem to think we live in Anti de Sitter space.”
As a working string theorist, active in conferences and paper-wise, I have a good grasp about what the community of people working on various aspects of holography and extensions of the conjecture made by Maldacena in 1997, actually believe or think.
No one of my colleagues believes that ”they live on AdS space”. Actually, all of them know we do not live in Anti de Sitter. These colleagues use Anti de Sitter and a theory of gravity defined on it to calculate observable quantities (correlation functions) of conformal field theories. By studying deviations from Anti de Sitter, these colleagues learn about quantum field theories that confine, spontaneously break symmetries, etc. They have developed set-ups in which various other non-perturbative effects are actually calculated.
Other part of the community have made important progress on the dynamics of black holes.
I believe that not recognising and not understanding these basic points leads to very misguided comments (I believed Sabine Hossenfelder understood these things) . Not appreciating this particular enterprise is, I believe, very narrow-minded.
I don’t think there’s really any incompatibility between what you and Sabine Hossenfelder have to say. Her “folks who seem to think we live in AdS” comment is clearly aimed at those who (like Farmelo) defend string theory as a theory of the real world by pointing to AdS/CFT. To the extent she offers a critique of the kind of research you describe, it’s not that no one should be doing it, but that too many people are doing it, and I think she is right about that. It’s not healthy for the field to be so dominated by one particular rather narrow line of research for the past twenty years.
IEHO the connection driving force is not the beauty of the connection between math and physics but the terseness of it. Short makes sweet.
Did Einstein “know” about the existence of Yang-Mills theory (in 1954) ?
I doubt it. Yang did talk about Yang-Mills at the IAS in February 1954, a year before Einstein’s death, but I believe at this point Einstein would not have been paying attention to what particle theorists were doing (Yang was trying to get a theory of the strong interactions).
Exactly what mathematical structures are to be investigated in lieu of experimental limitations, and who is supposed to be investigating these structures, the mathematicians, physicists, or both? Newton was able to be a mathematician and physicist of equal measure at the same time, not because he possessed superpowers, but because in the 1660’s the amount of material in the two subjects could be learned quicker than today. I don’t think physicists today would know enough about math to investigate the structures, and I don’t think mathematicians would know enough physics to know what structures to investigate.
My sentence was an attempt at humor, trying to express that while there is a large community studying fields in AdS, almost no one in this community works on explaining what this has to do with the real world. I know that a few exceptions exist, no need to tell me things I already know. But the vast majority of people in the area do calculations in AdS just because it’s simpler and they know how to do it, not because they actually know of any argument why it is useful to describe reality.
If I ask them why they work on this, they tell me they hope to learn something from it about dS. If you ask them a little more, they will admit that they have no reason to think the results transfer to dS. And don’t get me started again on the claim that it should work because both spaces are locally flat. It makes zero sense because all the benefits from working in AdS are non-local. And, needless to say, the world isn’t supersymmetric and not conformal and N isn’t infinity. These are mathematical fictions, not descriptions of anything in the real world.
This is not how science should work. And the reason why this is happening is obvious: They do it because they can, because they continue to get funding for it. It’s a waste of time and of money and it has to stop.
The reason I am phrasing this so bluntly is that I see a lot of hype in the media about AdS/CFT (sadly including otherwise reliable outlets like Physics Today and Nature) and they tend to not give the reader a clear impression about the promise of this research. It’s 99.99% hot air. It’s been pursued since 20 years and pretty much nothing has come out of it. (Except possibly for explaining why you do *not* need it in heavy ion collisions.) And this is the supposedly “greatest breakthrough” in the foundations of physics since the 1970s.
isn’t this Anti de Sitter space related work by you:
and this a notice about ongoing (since 2016) public funding you receive for this kind of work:
Would you deny for others
What you demand for yourself?
(U2, Crumbs from your table)
I find your tendency in this blog to praise any book (or any passage from a book like Farmelo’s) that exposes the deep connections between math and physics as a right track to move forward in unraveling the mysteries of nature really puzzling. I say this because from what I understood in Sabine’s book “Lost in Math” is that, not only relying on mathematical beauty did not lead to any new discovery about nature since the 70’s, but also what you call the “deep connection between math and physics” has not unraveled a single new principle about nature. It just created maybe new ways of dealing with problems in math or (at best) helped express old known facts in physics in a more abstract way.
I don’t understand what you mean by “Except possibly for explaining why you do *not* need it in heavy ion collisions.”
Why is it at all surprising that physics is best expressed in terms of math? Not only is it not surprising it’s necessarily true since math is just the *name* we apply to any kind of precise well-defined manipulation of concepts.
Or to put it another way can you even imagine a way in which the world could have been in which physics wasn’t best described via math? I mean imagine in some alternate universe we came up with some completely different set of rules/theories for predicting things. Whatever kind of manipulation we used to make predictions in that universe would also be called math. Sure, one could imagine that we couldn’t make any predictions about the world at all but in that case there wouldn’t be such a thing as physics. At a minimum, if we are capable of making any useful predictions about the world and our mental processes can be emulated by a Turing machine we could mathematically describe the process we used to make predictions and quantify it’s accuracy.
One can’t even argue it’s surprising that in many cases the math needed for physics was already developed. In a huge number of cases it isn’t true (and an area of math is only explored after it becomes apparent it is useful in physics). In the cases where it is true often the area of mathematics was already inspired by earlier physical theories and mathematicians explored a huge space of generalizations/modifications one of which happened to be useful later.
Indeed, for us to discover a physical theory SOMEONE has to think of the concepts it uses (without someone thinking up non-euclidean geometry first we wouldn’t have GR). Since mathematicians are also smart it would be shocking if physicists were always the first people to come up with those generalizations.
Dear Sabine, dear Peter,
a very brief message given the conversation started above.
In this message, I am referring the work on AdS/CFT and many of its variations. I see what a majority of string theorist are doing as a way of learning about Quantum Field Theories in general (different dimensions, different amount of global symmetries). I very much fail to see this as a not-worthy enterprise. Also, I fail to see the hype in the media about this research (but may be this is due to the fact that I do not follow the media).
I find the criticism useful. But when Sabine writes about the research on AdS/CFT:
”It’s 99.99% hot air. It’s been pursued since 20 years and pretty much nothing has come out of it. ”
I feel that she does not know and did not read 99-per cent of the works in this area to write this comment. I am unable to read all the papers on AdS/CFT, but on those I read and check calculations, my opinion is exactly the opposite of ‘hot air’.
I refrain to believe that the great majority of my colleagues are working on this just because they get the funding to do so. I very much refrain to believe that the daily discussion and calculations with colleagues are just a ‘charade’ and that we should know that is 99.99 per cent hot air.
I find hard to believe that most of the people around me are idiots or perverse minds who are not interested in science, but only on their next grant. My empirical observations of colleagues indicate exactly the opposite!
On Sabine’s paragraph
” It makes zero sense because all the benefits from working in AdS are non-local. And, needless to say, the world isn’t supersymmetric and not conformal and N isn’t infinity. These are mathematical fictions, not descriptions of anything in the real world.”
Our viewpoints on this cannot be more divergent. I believe that she is just wrong. I prefer not to comment as it would make this posting too long.
There’s no reason physicists can’t learn math or mathematician’s can’t learn physics. Einstein (with some help) learned Riemannian geometry. Witten not only learned a lot of mathematics, he created very significant new mathematics. There is a whole field of “mathematical physicists” who work in between the two subjects.
Yes, investigations of the relation of math and physics since the 1970s have not led to significant advance in fundamental physics theory, but neither has anything else. Your choices at this point are to give up or pursue whatever you think is the most promising path, in full knowledge that that path has not recently been successful.
I don’t see the failures of string theory, supersymmetry, etc. as due to people mistakenly pursuing mathematical beauty. After initial ideas with some beauty, those subjects quickly degenerated into a complicated and ugly mess (endpoint the landscape) as one tried to reconcile them with known physics. If people actually had been pursuing mathematical beauty, this would have caused them to abandon these subjects long ago.
What’s surprising is not that fundamental physics is expressed in terms of math, but that its deepest ideas are closely related to the deepest ideas in mathematics. For example:
GR and Geometry
The Dirac equation
Connections, curvature and Yang-Mills theory
The relations between quantum theory and representation theory (see my recent book)
I understand that Witten created marvelous new mathematical structures, among his many achievements, his construction of topological quantum field theories stands out as his most influential. But, my understanding is that TQFT hasn’t really had much of an impact on fundamental physics and is mostly studied by mathematicians. That’s exactly my point, one doesn’t know which mathematical structures to study that would lead to significant advances on the fundamental physics front.
Yes, there is no clear path saying “study this mathematical structure, you’ll find the right idea for how to get a better theory than the SM +GR”. There is also no other clear path to such a better theory, so this may be more promising than any alternatives.
Of course you do not want to believe what I say and neither want your colleagues. But no need to believe me. This is science after all. Look at the papers that have been written and list what observations were correctly predicted. The answer is: None. That’s what has come out of it.
You don’t have to dig deep for hype, here are some recent examples:
“I believe that she is just wrong.”
Hahaha. No shit.
Look, that’s not how it works. Science isn’t about beliefs. There is no reason to think that the limit Lambda to zero is continuous. In fact there are all kinds of reasons to think it is not, starting with the very fact that you do calculations in AdS because you need Lambda to be smaller than zero.
I did not say that it’s not a worthy enterprise. Please do not put words into my mouth I didn’t use.
Yes, I know what I am talking about. Glad to see you figured that.
“” It makes zero sense because all the benefits from working in AdS are non-local. And, needless to say, the world isn’t supersymmetric and not conformal and N isn’t infinity. These are mathematical fictions, not descriptions of anything in the real world.”
Our viewpoints on this cannot be more divergent. I believe that she is just wrong. I prefer not to comment as it would make this posting too long.”
I find it hard to believe that this is not a tongue-in-cheek comment.
Maybe that’s enough about AdS/CFT. It’s not even emphasized that much in Farmelo’s book, where his take on the current state of things is more Arkani-Hamed-centric, with the Amplituhedron the centerpiece of the best case for a current math/physics topic on the right track to success.
Is the talk at IAS over ?
Event is still going on, just now (4:25) coming back from break. Will go on until 5:45.
“I understand that Witten created marvelous new mathematical structures, among his many achievements, his construction of topological quantum field theories stands out as his most influential. But, my understanding is that TQFT hasn’t really had much of an impact on fundamental physics and is mostly studied by mathematicians.”
Actually TQFT and its “holographic dual” 2D CFT have been enormously influential and productive in condensed matter physics, where these frameworks are used to describe actual experiments such as the fractional quantum Hall effect (FQHE). TQFT was used by Shou-Cheng Zhang and collaborators to provide the “composite boson theory” of the FQHE, a simple mean-field framework that allows one to “derive” key results like Laughlin’s many-body wave function. More recently (mid-90s onwards), much of Alexei Kitaev’s work on spin liquids and topological quantum computation is rooted in CFT representation theory. This is now driving large-scale experimental efforts funded by Microsoft (Station Q at UCSB and Copenhagen).
Suffice to say we cm physicists do not believe that “fundamental physics” can be done only in the service of unification! 🙂
Here is the Dijkgraaf/Witten conversation:
Is Edward acknowledging from 12:00 onwards that the AdS/CFT correspondence, and its relation to emergent spacetime, is (or might be) wrong?
It´s hard to say what word he uses around 12:33 (“It colours? a lot of our thinking…)
Thanks for any help provided.
Regarding your comment that the book’s defense of string theory is “trust certain famous theorists”, I think the “trust famous theorists” attitude is one of the big problems with HEP today.
For a concrete example, Lenny Susskind is writing papers that use quantum information theory in what seem to me more and more nonsensical ways, and (a) there are some people paying attention to him and building on these papers, and (b) very few or no high energy physicists are saying that these papers can’t possibly be correct.
Hi Peter Shor, I’m curious what makes you think Susskind’s recent papers “can’t possibly be correct.” They seem so vague to me that they can’t be right, but I’m interested to know what is concrete enough in them to be wrong.
Thanks. I added a link to the conversation, some extracts and some comments. As for the part you point to, I can’t tell what Witten’s final “it might be wrong” is supposed to refer to. Unlikely he means the Maldacena conjecture, perhaps something more general about current expectations concerning “emergent space-time”.
I agree that the “trust certain famous theorists” argument is highly problematic. For me, one of the main reasons I got interested in science and math was that it was not about trusting authority figures. If you were willing to put in the effort, you could learn a subject and follow the arguments, and once you did this you could evaluate for yourself the evidence for a claim.
My problem with much of the claims by Susskind of recent years is more that I can’t even figure out what he is claiming, a rather extreme version of the “not even wrong” phenomenon.
Nima Arkani-Hamed is highly influential, with much of this book channeling his (current) point of view. However, if you look back at his career, you find equal enthusiasm for ideas that didn’t work out (e.g. large extra dimensions), and he describes himself as a not-so-reliable “serial ideologue”, here
Unlike Susskind and Arkani-Hamed, Witten is someone who tries to be careful and reliable in what he claims. To me, the conversation with Dijkgraaf indicates that, while he’s still unwilling to give up on the dream of 1984, he’s now all too aware that things have not gone well for it, that he has no “scientifically convincing” argument for his hopes, nor any prospects for getting one anytime soon.
thanks for the link and your comments.
After listening again to what he says, I agree with you that he´s most probably referring to ideas about emergent spacetime.
I tend to think the same as him there, that spacetime is emergent.
And I have my own idea of what is behind it, but that´s not for this post.
He´s very careful with his words, but it seems to me that he doesn´t like any of the ideas that are nowadays floating around about that issue.
I am extremely skeptical of ER=EPR. Susskind says
“ER=EPR tells us that the immensely complicated network of entangled subsystems that comprises the universe is also an immensely complicated (and technically complex) network of Einstein-Rosen bridges.”
I don’t see how you can say that entanglement is the same thing as ER bridges unless you mean something completely different by either “entanglement” or “ER bridges” than Schrödinger meant, or Einstein and Rosen meant. Entanglement is a property of quantum mechanics, ER bridges are a property of general relativity, and as far as we know quantum field theory works fine without general relativity, and vice versa.
And Google Scholar says that this paper has 745 citations, which is two thirds as many as the AMPS (Black Holes: Complementarity or Firewalls) paper, which actually contains real, potentially correct, ideas.
With all due respect to Dirac, it was von Neumann who put Quantum Mechanics on a sound mathematical basis. Dirac, among others, were the ones trying to make sense of the physics, and found mathematical formalisms that could help — as distinct from the essentially infinite sample of such formalisms that don’t. Von Neumann pointed out logical inconsistencies in what Dirac proposed, despite it being more “beautiful” and “elegant” than what von Neumann proposed in its place that actually made mathematical sense. See, e.g., https://plato.stanford.edu/entries/qt-nvd/. (And Dirac’s later obsession with numerology should serve as a warning about losing that perspective.) Never mind that the mathematically rigorous version requires infinite dimensional Hilbert spaces to make it work — not quite what one would consider a “physical” concept. Is that “mathematically beautiful”? Or does it just work, so we sweep the awkwardness under the rug?
As mentioned previously, Einstein first had physical intuition about what was happening; he then had to find a way to describe that in a consistent way that could be measured — which then helped to elucidate further implications of those insights, as well as advancing mathematics (e.g., differential geometry). Not the other way around.
Your own recent book seems like a slightly lesser version of what Sabine Hossenfelder and even you are critiquing. It seemed to me a good, if rather abstract, explanation of “Here’s what they mean when they say ‘XYZ'”, from a mathematician’s point of view, but only tangentially related to any underlying physics. (Reminds me somewhat of the book General Relativity for Mathematicians by Sachs and Wu. : -) As with most of modern fundamental theoretical physics — even some of what is described in low-dimensionality solid state physics — my response is essentially “That’s interesting, in an abstract conceptual sense, but … So What?” In terms used by actual practitioners of Computer Science (i.e., programmers), much of what is described appears to be a kludge on top of a kludge on top of a kludge — but at least you get (approximately) the right answers. Unfortunately, that seems to apply more broadly.
The mathematics on which most of physics is based evolved as a way to describe things that can be expressed as differentiable (analytic) functions over smooth manifolds compatible with Euclidean space (locally if not globally) — but even there the mental gymnastics required to describe that in a self-consistent way seems far divorced from physical reality. Just the issue of differentiating with respect to time in a GR (not just Minkowski) spacetime, when time itself is a dynamical variable “in the real world”, is just glossed over. And then the question: is it continuous, to the level we need to actually describe underlying fundamental physics? How does any of today’s mathematics handle it if it’s not?
Likewise, almost nothing that we are currently observing in astrophysics can be expressed concretely using any analytical formalism — only arbitrary, custom designed computational models calculated using Markov approaches, from which one selects “closest fits” based on semi-physical parameters and estimations — and often “matched” to data by machine learning algorithms. (A troubling corollary: the people who found significance in Bode’s law – the supposed magical spacing of (then-known) planets in our solar system that turned out to be nonsense.) So I have trouble understanding your faith that some deep “mathematical mysticism” will lead to any better understanding of physics than we already have (or don’t).
I also find the idea of “ER = EPR” to be a bit far fetching. But I think the idea is that classical spacetime is emergent from an underlying entangled state (of some unknown entity). Not sure how they could make it work but it is probably not true that entanglement is wormhole as entanglement could be between degrees of freedom of a single particle, and wormhole is between two different spatial locations.
It’s very unclear to me what “ER=EPR” actually is supposed to mean, other than that it can’t mean what it says since, as Peter Shor points out, it claims an equality of two things that in our currently understood best theories (QM and GR), have nothing at all to do with each other. As near as I can figure out, what it really is is a slogan for a speculative hope: “let’s find a quantum theory of gravity in which these two things are related”, part of the general program of “let’s find a quantum theory of gravity in which space-time emerges from quantum entanglement”.
All attempts on my part to understand what the current state of this program is have left me with the impression that, while this has been an increasingly hot topic among “leading theorists” for a decade now, it hasn’t managed to get much beyond its original motivation based on some crude aspects of what happens in AdS/CFT. The main activity seems to be the study of toy models, with this research leading to the realization that the toy models don’t actually in any simple way embody the hoped for properties. Some of the people involved in this have a history of misleading the public by promoting outrageous hype about string theory, and the current public promotion of things like “ER=EPR” is starting to look like more of the same.
Under the circumstances, to me it seems best to try and ignore all this for now, and wait and see if anything solid emerges from the cloud of “emergent gravity” hype.
You’re missing the point I keep trying to make about the role of mathematics in new ideas about fundamental physics. This has nothing to do with mathematical rigor (other than the general point that you really should try and be clear about exactly what you are talking about, see above comment about ER=EPR: the problem there is not lack of rigor, but lack of any clear meaning at all).
Let me give three examples of what I am talking about:
1. Einstein’s use of Riemannian geometry to formulate GR.
2. Dirac’s definition of quantization as taking Poisson brackets to commutators, i.e. as a Lie algebra representation.
3. Dirac’s introduction of Clifford algebras and spinors, allowing the construction of the Dirac operator and a square root of the Laplacian.
All three of these were huge advances in our understanding of fundamental physics, based upon the introduction of new and surprising deep mathematical ideas, not “physical intuition”. I think the expectation that further such advances are possible and will have the same nature is quite rational. In particular, the mathematics behind parts 2. and 3. is still not completely understood (e.g. the role of the Dirac operator in representation theory), and a deeper understanding may very well lead to a deeper understanding of fundamental physics.
I see that Urs Schreiber thinks it’s a good idea to put up an edited version of what I write here on Twitter, see
Note how he edits out the rest of the sentence he highlights, the part where I write:
“and wait and see if anything solid emerges from the cloud of “emergent gravity” hype.”
By the way, to bring this back to the topic of the post. One reason for skepticism about “ER=EPR” and such things is the lack of any significant deep mathematical idea behind it. This line of research seems to be orthogonal to the deep mathematical ideas about symmetry that have been so successful in leading to the standard model, and instead often seems to be based on rather simple minded mathematics.
What do you think of Dijkgraaf’s comment: “…because in some sense it’s an integral part of the theories that we already are using.” ?
Is this the old story of “string theory is a quantum theory” sort of thing? Or what do you think he’s alluding to?
I know of exactly zero theories we use in HEP to describe nature that string theory is a part of.
This is the same argument David Gross and others have been using for years when challenged about the failure of string theory unification. It’s basically
“The AdS/CFT conjecture suggests that the superstring on AdS5 x S^5 is dual to N=4 super Yang-Mills on S^4. So, in this case, a string theory is an alternative formulation of a specific QFT, and one can find other examples of this kind of QFT/string theory duality. So, string theory is closely related to (some) QFTs, and so you can’t argue that only QFT is relevant, not string theory.”
One problem with this argument is that the relation to QFT is not to Standard Model QFTs known to be fundamental, but to QFTs with rather different properties (i.e. conformal invariance, no asymptotic freedom). Hopes that this could be extended to get a string theory dual of QCD have not worked out. There seems zero reason to believe in a string theory dual of the weakly-coupled parts of the SM (this would have to be some strongly-coupled string theory we have no evidence for or theory of).
The other problem is that, as Witten immediately recognizes and notes in his response, what people are doing when they are making this argument is implicitly giving up on string theory unification. When I and others argue to string theorists that string theory unification is a failure and they respond “string theory has some connection to QCD”, they are acknowledging they have no positive argument for string theory unification and are trying to talk about something else. Witten responds to Dijkgraaf that he doesn’t want to do this and implicitly give up on string theory unification, just turning the string theory research program into one focused on hope for a better calculational method to deal with certain strongly-coupled quantum systems.
The original qualitative arguments for “ER=EPR” (back in arXiv:1306.0533) left me completely bewildered. They would equally well imply that a wormhole exists between the two halves of a Werner system, or between any two correlated toy bits in the Spekkens model, which is absurd. Now, there can certainly be a big gap in solidity between the original motivations and later results, but here, I feel like we’re still waiting to see what those “later results” actually are.
Blake Stacey/Peter Shor,
Urs Schreiber explains here
that ER=EPR is a “Zen koan”, or maybe a “koan-like slogan”, and Susskind’s paper about it is “uninhibited vague brainstorming”.
Will Kinney comments here
Referring to a folk theorem stating there’s one subject in math you always avoid that turns out to be the relevant one for your next paper, Robbert Dijkgraaf asks E. Witten:
I naively conclude from this revealing interview that thinking abstractly (what could be the proper geometric framework to define quantum Yang-Mills-Higgs theory in 4D space-time for instance) might be the quality of mathematicians while computing formally (entropy of “entangling surfaces” to probe a “bulk geometry” in the AdS/CFT conjecture context) is mostly the privilege of physicists.
“1.Einstein’s use of Riemannian geometry to formulate GR.
All three of these were huge advances in our understanding of fundamental physics, based upon the introduction of new and surprising deep mathematical ideas, not “physical intuition”.”
Einstein’s Zurich Notebook* seems to indicate that the basic idea of objects following a geodesic on a curved surface had a lot of physical intuition involved–some of it based on previous classical physics results, but that is how intuition is developed, from experience.
Yes, it does seem Einstein’s original motivation for GR could be described as “physical intuition”. I think though that if you look at the history, it’s pretty clear that he would never have gotten off the ground, developed a real theory and found the equations of GR, without the mathematics of Riemannian geometry.
Off topic but why nothing about the death of Gell-Mann?
See previous posting.
I’m a big fan of your blog. I also really enjoy reading physics and math books that are geared to a more general audience (although I have a PhD in physics, I don’t want to have to work too hard to read a book before bedtime). I’ve gotten some good book ideas from reading your blog in the past. I’m wondering if you’d consider putting another recommendation section on your blog for books that you’ve enjoyed (perhaps categorized by subject) – and perhaps link them to reviews you’ve done, if you have. It’d be really nice to have one place to go to find a good physics/math book when I’m in the mood for one.
If you select posts by category, choosing the “Book Reviews” category
gives 105 postings about books, mostly book reviews, going back to 2004. Pretty much all of these are books about physics and or math. Mostly I write about something because I think it’s interesting enough to be worth reading. You should take a look at the review first, since in a few cases there’s a negative reason I’m writing about the book, definitely not recommending it to others (for a recent example, don’t go out and get Lee McIntyre’s “The Scientific Attitude”….)
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