I was asked to review Lee Smolin’s The Trouble With Physics by New Scientist. The review has now appeared, although with a couple of drawbacks. Most obviously, only subscribers can read it. But more importantly, they have some antiquated print-journal notion of a “word limit,” which in my case was about 1000 words. When I started writing the review, I kind of went over the limit. By a factor of about three. This is why the Intelligent Designer invented blogs; here’s the review I would have written, if the Man hadn’t tried to stifle my creativity. (Other reviews at Backreaction and Not Even Wrong; see also Bee’s interview with Lee, or his appearance with Brian Greene on Science Friday.)
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It was only after re-reading and considerable head-scratching that I figured out why Lee Smolin’s The Trouble With Physics is such a frustrating book: it’s really two books, with intertwined but ultimately independent arguments. One argument is big and abstract and likely to be ignored by most of the book’s audience; the other is narrow and specific and part of a wide-ranging and heated discussion carried out between scientists, in the popular press, and on the internet. The abstract argument — about academic culture and the need to nurture speculative ideas — is, in my opinion, important and largely correct, while the specific one — about the best way to set about quantizing gravity — is overstated and undersupported. It’s too bad that vociferous debate over the latter seems likely to suck all the oxygen away from the former.
Fundamental physics (for want of a better term) is concerned with the ultimate microscopic laws of nature. In our current understanding, these laws describe gravity according to Einstein’s general theory of relativity, and everything else according to the Standard Model of particle physics. The good news is that, with just a few exceptions (dark matter and dark energy, neutrino masses), these two theories are consistent with all the experimental data we have. The bad news is that they are mutually inconsistent. The Standard Model is a quantum field theory, a direct outgrowth of the quantum-mechanical revolution of the 1920’s. General relativity (GR), meanwhile, remains a classical theory, very much in the tradition of Newtonian mechanics. The program of “quantum gravity” is to invent a quantum-mechanical theory that reduces to GR in the classical limit.
This is obviously a crucially important problem, but one that has traditionally been a sidelight in the world of theoretical physics. For one thing, coming up with good models of quantum gravity has turned out to be extremely difficult; for another, the weakness of gravity implies that quantum effects don’t become important in any realistic experiment. There is a severe conceptual divide between GR and the Standard Model, but as a practical matter there is no pressing empirical question that one or the other of them cannot answer.
Quantum gravity moved to the forefront of research in the 1980’s, for two very different reasons. One was the success of the Standard Model itself; its triumph was so complete that there weren’t any nagging experimental puzzles left to resolve (a frustrating situation that persisted for twenty years). The other was the appearance of a promising new approach: string theory, the simple idea of replacing elementary point particles by one-dimensional loops and segments of “string.” (You’re not supposed to ask what the strings are made of; they’re made of string stuff, and there are no deeper layers.) In fact the theory had been around since the late 1960’s, originally investigated as an approach to the strong interactions. But problems arose, including the unavoidable appearance of string states that had all the characteristics one would expect of gravitons, particles of gravity. Whereas most attempts to quantize gravity ran quickly aground, here was a theory that insisted on the existence of gravity even when we didn’t ask for it! In 1984, Michael Green and John Schwarz demonstrated that certain potentially worrisome anomalies in the theory could be successfully canceled, and string mania swept the particle-theory community.
In the heady days of the “first superstring revolution,” triumphalism was everywhere. String theory wasn’t just a way to quantize gravity, it was a Theory of Everything, from which we could potentially derive all of particle physics. Sadly, that hasn’t worked out, or at least not yet. (String theorists remain quite confident that the theory is compatible with everything we know about particle physics, but optimism that it will uniquely predict the low-energy world is at a low ebb.) But on the theoretical front, there have been impressive advances, including a “second revolution” in the mid-nineties. Among the most astonishing results was the discovery by Juan Maldacena of gauge/gravity duality, according to which quantum gravity in a particular background is precisely equivalent to a completely distinct field theory, without gravity, in a different number of dimensions! String theory and quantum field theory, it turns out, aren’t really separate disciplines; there is a web of dualities that reveal various different-looking string theories as simply different manifestations of the same underlying theory, and some of those manifestations are ordinary field theories. Results such as this convince string theorists that they are on the right track, even in the absence of experimental tests. (Although all but the most fervent will readily agree that experimental tests are always the ultimate arbiter.)
But it’s been a long time since the last revolution, and contact with data seems no closer. Indeed, the hope that string theory would uniquely predict a model of particle physics appears increasingly utopian; these days, it seems more likely that there is a huge number (10500 or more) phases in which string theory can find itself, each featuring different particles and forces. This embarrassment of riches has opened a possible explanation for apparent fine-tunings in nature — perhaps every phase of string theory exists somewhere, and we only find ourselves in those that are hospitable to life. But this particular prediction is not experimentally testable; if there is to be contact with data, it seems that it won’t be through predicting the details of particle physics.
It is perhaps not surprising that there has been a backlash against string theory. Lee Smolin’s The Trouble With Physics is a paradigmatic example, along with Peter Woit’s new book Not Even Wrong. Both books were foreshadowed by Roger Penrose’s massive work, The Road to Reality. But string theorists have not been silent; several years ago, Brian Greene’s The Elegant Universe was a surprise bestseller, and more recently Leonard Susskind’s The Cosmic Landscape has focused on the opportunities presented by a theory with 10500 different phases. Alex Vilenkin’s Many Worlds in One also discusses the multiverse, and Lisa Randall’s Warped Passages enthuses over the possibility of extra dimensions of spacetime — while Lawrence Krauss’s Hiding in the Mirror strikes a skeptical note. Perhaps surprisingly, these books have not been published by vanity presses — there is apparently a huge market for popular discussions of the problems and prospects of string theory and related subjects.
Smolin is an excellent writer and a wide-ranging thinker, and his book is extremely readable. He adopts a more-in-sorrow-than-in-anger attitude toward string theory, claiming to appreciate its virtues while being very aware of its shortcomings. The Trouble with Physics offers a lucid introduction to general relativity, quantum mechanics, and string theory itself, before becoming more judgmental about the current state of the theory and its future prospects.
There is plenty to worry or complain about when it comes to string theory, but Smolin’s concerns are not always particularly compelling. For example, there are crucially important results in string theory (such as the fundamental fact that quantum-gravitational scattering is finite, or the gauge/gravity duality mentioned above) for which rigorous proofs have not been found. But there are proofs, and there are proofs. In fact, there are almost no results in realistic quantum field theories that have been rigorously proven; physicists often take the attitude that reasonably strong arguments are enough to allow us to accept a claim, even in the absence of the kind of proof that would make a mathematician happy. Both the finiteness of stringy scattering and the equivalence of gauge theory and gravity under Maldacena’s duality are supported by extremely compelling evidence, to the point where it has become extremely hard to see how they could fail to be true.
Smolin’s favorite alternative to string theory is Loop Quantum Gravity (LQG), which has grown out of attempts to quantize general relativity directly (without exotica such as supersymmetry or extra dimensions). To most field theorists, this seems like a quixotic quest; general relativity is not well-behaved at short distances and high energies, where such new degrees of freedom are likely to play a crucial role. But Smolin makes much of one purported advantage of LQG, that the theory is background-independent. In other words, rather than picking some background spacetime and studying the propagation of strings (or whatever), LQG is formulated without reference to any specific background.
It’s unclear whether this is really such a big deal. Most approaches to string theory are indeed background-dependent (although in some cases one can quibble about definitions), but that’s presumably because we don’t understand the theory very well. This is an argument about style; in particular, how we should set about inventing new theories. Smolin wants to think big, and start with a background-independent formulation from the start. String theorists would argue that it’s okay to start with a background, since we are led to exciting new results like finite scattering and gauge/gravity duality, and a background-independent formulation will perhaps be invented some day. It’s not an argument that anyone can hope to definitively win, until the right theory is settled and we can look back on how it was invented.
There are other aspects of Smolin’s book that, as a working physicist, rub me the wrong way. He puts a great deal of emphasis on connection to experimental results, which is entirely appropriate. However, he tends to give the impression that LQG and other non-stringy approaches are in close contact with experiment in a way that string theory is not, and I don’t think there’s any reasonable reading on which that is true. There may very well be certain experimental findings — which haven’t yet happened — that would be easier to explain in LQG than in string theory. But the converse is certainly equally true; the discovery of extra dimensions is the most obvious example. As far as I can tell, both string theory and LQG (and every other approach to quantizing gravity) are in the position of not making a single verifiable prediction that, if contradicted by experiment, would falsify the theory. (I’d be happy to hear otherwise.)
Smolin does mention a number of experimental results that have already been obtained, but none of them is naturally explained by LQG any more than by string theory, and most of them are, to be blunt, likely to go away. He mentions the claimed observation that the fine-structure constant is varying with time (against which more precise data has already been obtained), certain large-angle anomalies in the cosmic microwave background anisotropy, and the possibility of large-scale modifications of general relativity replacing dark matter. (Bad timing on that one.) I don’t know of any approach to quantum gravity that firmly predicts (or even better, predicted ahead of time) that any of these should be true. That’s the least surprising thing in the world; gravity is a weak force, and most of the universe is in the regime where it is completely classical.
Smolin also complains about the tendency of string theorists to hype their field. It is hard to argue with that; as a cosmologist, of course, it is hard to feel morally superior, either. But Smolin does tend to project such a feeling of superiority, often contrasting the careful and nuanced claims of LQG to the bombast of string theory. Yet he feels comfortable making statements such as (p. 232)
Loop quantum gravity already has elementary particles in it, and recent results suggest that this is exactly the right particle physics: the standard model.
There are only two ways to interpret this kind of statement: either (1) we have good evidence that quantum spacetime alone, without additional fields, supports excitations that have the right kinds of interactions and quantum numbers to be the particles of the Standard Model, which would be the most important discovery in physics since the invention of quantum mechanics, or (2) it’s hype. Time will tell, I suppose. The point being, it’s perfectly natural to get excited or even overenthusiastic when one is working on ideas of fantastic scope and ambition; at the end of the day, those ideas should be judged on whether they are right or wrong, not whether their proponents were insufficiently cautious and humble.
To date, the string theorists are unambiguously winning the battle for support within the physics community. Success is measured primarily by faculty positions and grant money, and these flow to string theorists much more than to anyone pursuing other approaches to quantum gravity. From an historical perspective, the unusual feature of this situation is that there are any resources being spent on research in quantum gravity; if string theory were suddenly to fall out of favor, it seems much more likely that jobs and money would flow to particle phenomenology, astrophysics, or other areas of theory than to alternative approaches to quantum gravity.
It seems worth emphasizing that the dominance of string theory is absolutely not self-perpetuating. When string theorists apply for grants, they are ultimately judged by program officers at the National Science Foundation or the Department of Energy, the large majority of whom are not string theorists. (I don’t know of any who are, off the top of my head.) And when string theorists apply for faculty jobs, it might very well be other string theorists who decide which are the best candidates, but the job itself must be approved by the rest of the department and by the university administration. String theorists have somehow managed to convince all of these people that their field is worthy of support; I personally take the uncynical view that they have done so through obtaining interesting results.
Smolin talks a great deal about the need for physics, and academia more generally, to support plucky upstart ideas and scholars with the courage and vision to think big and go against the grain. This is a larger point than the specific argument about how to best quantize gravity, and ultimately far more persuasive; it is likely, unfortunately, to be lost amidst the conflict between string theory and its discontents. Faculty positions and grant money are scarce commodities, and universities and funding agencies are naturally risk-averse. Under the current system, a typical researcher might spend five years in graduate school, three to six as a postdoc, and another six or seven as an assistant professor before getting tenure — with an expectation that they will write several competent papers in every one of those years. Nobody should be surprised that, apart from a few singular geniuses, the people who survive this gauntlet are more likely to be those who show technical competence within a dominant paradigm, rather than those who will take risks and pursue their idiosyncratic visions. The dogged pursuit of string theory through the 1970’s by Green and Schwarz is a perfect example of the ultimate triumph of the latter approach, and Smolin is quite correct to lament the lack of support for this kind of research today.
In the real world, it’s difficult to see what to do about the problem. I would be happy to see longer-term postdocs, or simply fewer postdocs before people move on to assistant professorships. But faculty positions are extremely rare — within fundamental theory, a good-sized department might have two per decade, and it would be hard to convince a university to take a long-shot gamble on someone outside the mainstream just for the greater good of the field as a whole. And a gamble it would certainly be. Smolin stacks the deck by contrasting the “craftsmen” who toil within string theory to the “seers” who pursue alternatives, and it’s pretty obvious which is the more romantic role. Many physicists are more likely to see the distinction as one between “doers” and “dreamers,” or even (among our less politic colleagues) between “scientists” and “crackpots.”
To be clear, the scientists working on LQG and other non-stringy approaches to quantum gravity are not crackpots, but honest researchers tackling a very difficult problem. Nevertheless, for the most part they have not managed to convince the rest of the community that their research programs are worthy of substantial support. String theorists are made, not born; they are simply physicists who have decided that this is the best thing to work on right now, and if something better comes along they would likely switch to that. The current situation could easily change. Many string theorists have done interesting work in phenomenology, cosmology, mathematical physics, condensed matter, and even loop quantum gravity. If a latter-day Green and Schwarz were to produce a surprising result that convinced people that some alternative to string theory were more promising, it wouldn’t take long for the newcomer to become dominant. Alternatively, if another decade passes without substantial new progress within string theory, it’s not hard to imagine that people will lose interest and switch to other problems. I would personally bet against this possibility; string theory has proved to be a remarkably fruitful source of surprising new ideas, and there’s no reason to expect that track record to come to a halt.
Smolin is right in the abstract, that we should try to nurture a diversity of approaches to difficult questions in physics, even if his arguments on the specific example of string theory and its competitors are less compelling. But he is also right that string theorists are not always as self-critical as they could be, and can even occasionally be a mite arrogant (although I haven’t found this quality to be rare within academia). The best possible consequence of the appearance of The Trouble with Physics and similar books would be that physicists of all stripes are moved to take an honest look at the strengths and weaknesses of their own research programs, and to maintain an open mind about alternatives. (The worst possible consequence would be for large segments of the public, or the student population, or even physicists in other specialties, to misunderstand why string theorists find their field so compelling.) Sometimes a little criticism can be a healthy thing.
not that it’s worth anything, but I think some of the comments here illustrate one of the reasons why there has been a backlash against string theory. As Dr. Carroll has pointed out, LQG is not neccesarily better supported experimentally than string theory is, and I doubt many people outside of particle theory would really think it would be an improvement if as many people were working on LQG as string threory. Of course, many physicists would be absolutely delighted if some form of LQG and some form of string theory produced different predictions for any parameter related to elementary particles or cosmology.
However, a couple of commenters here, instead of suggesting that one needs to clarify the differences between the theories, want to include both of them in an even broader theory, which would seem to be even less predictive. Certainly this may be doable, but the attitude that it is better to make a theory more general and abstract than more specific and concrete is one of the things that keeps me (and I imagine many others) from being particularly enthusiastic about string theory at the present moment.
While string theorists (and “high-end” particle theorists generally) play lip service to the need for experiment, it appears the disconnect between theory and experiment is particularly large for particle physics. In cosmology, for example, most theorists these days seem to spend at least some time getting their hands dirty with experimental data, or at least do some combination of “fundamental” and “applied” theory. By contrast, there seem to be more full-time, narrowly focused string theorists, who are solely interested in the “fundamental” questions, and aren’t intersted in whether such-and-such experiment has measured the decay width of the XYZ baryon.
In part, I expect this is because the field of high-energy physics is starved for unexplained data, but it seems to me there may also be a vicious feedback cycle operating. If people working on string theory/LQG/etc. do not ever work on data from experiments, they can become convinced nothing interesting happens below the planck scale. Then they will be even less interested in any specific current experiment, and they will not encourage younger researchers to take an interest in actual data. With less people poking at the data, there is more of a chance that something strange might be missed, further encouraging the theorists’ notion that there is nothing interesting in the experimental data, and widening the gulf between theory and experiment.
I’m not sure if this is actually happening, but the enthusiasm of string theory for abstract notions of “elegance” always gives me pause.
I’m sadly “without formal training” in philosophy, but… I believe most working scientists are positivists to a large degree. To quote a physics professor from the place Sean just left, the U of C: “The philosopher wants to complicate things, expand on nothing.”
Not that I entirely agree with that statement. Most scientists don’t spend a whole lot of time thinking about philosophy, and there is a role for those who do philosophy in a scientific way. Work on interpretations of quantum mechanics that are suitable for quantum cosmology and whatnot. But I admit I have a dim view of a lot of philosophy.
strategichamlet– I try not to criticize people for making statements on the basis that they don’t have formal training; I’d prefer to judge statements on whether they are right or wrong. I will sometimes criticize people for imagining that formal training isn’t useful, and then going and making wrong statements.
But, more relevantly, I don’t see what my statements about string theory have to do with positivism. Why do you say that?
‘As far as I can tell, both string theory and LQG (and every other approach to quantizing gravity) are in the position of not making a single verifiable prediction that, if contradicted by experiment, would falsify the theory. (I’d be happy to hear otherwise.)’ – Sean
This is very much what Eddington wrote about the situation back in 1921:
‘It has been said that more than 200 theories of gravitation have been put forward; but the most plausible of these have all had the defect that they lead nowhere and admit of no experimental test.’ – Sir Arthur Stanley Eddington, ‘Space Time and Gravitation’, Cambridge University Press, 1921, p64.
Despite the to ‘admit of … experimental test’, we hear:
‘String theory has the remarkable property of predicting gravity.’ – Edward Witten, M-theory originator, Physics Today, April 96.
As for LQG:
‘In loop quantum gravity, the basic idea is … to … think about the holonomy [whole rule] around loops in space. The idea is that in a curved space, for any path that starts out somewhere and comes back to the same point (a loop), one can imagine moving along the path while carrying a set of vectors, and always keeping the new vectors parallel to older ones as one moves along. When one gets back to where one started and compares the vectors one has been carrying with the ones at the starting point, they will in general be related by a rotational transformation. This rotational transformation is called the holonomy of the loop. It can be calculated for any loop, so the holonomy of a curved space is an assignment of rotations to all loops in the space.’ – P. Woit, Not Even Wrong, Cape, London, 2006, p189.
Surely this is compatible with Yang-Mills quantum field theory where the loop is due to the exchange of force causing gauge bosons from one mass to another and back again.
Over vast distances in the universe, this predicts that redshift of the gauge bosons weakens the gravitational coupling constant. Hence it predicts the need to modify general relativity in a specific way to incorporate quantum gravity: cosmic scale gravity effects are weakened. This indicates that gravity isn’t slowing the recession of matter at great distances, which is confirmed by observations. As Phil Anderson said earlier on this blog, “the flat universe is just not decelerating, it isn’t really accelerating …”
– http://blogs.discovermagazine.com/cosmicvariance/2006/01/03/danger-phil-anderson
nc, I am pretty sure that the prediction of gravity is not likely to be contradicted by experiment.
Ho ho, ha ha …
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Sean,
I hope Lee will find time to respond to this himself, but here are some comments on part of your review.
I think you misrepresent and misunderstand the points that Smolin was making about string scattering amplitudes and gauge/gravity duality. He was not objecting to a lack of mathematical rigor, but to overhyping and misrepresentation of results, something that he himself was taken in by, even though he considered himself a serious student and researcher in string theory. You’re engaging in precisely the behavior that he finds problematic:
“Both the finiteness of stringy scattering and the equivalence of gauge theory and gravity under Maldacena’s duality are supported by extremely compelling evidence, to the point where it has become extremely hard to see how they could fail to be true.”
First of all, string scattering amplitudes are not even conjecturally finite in string perturbation theory. The conjecture is that the perturbation expansion is divergent, at best an asymptotic series. At any fixed coupling this series gives an infinite answer. The standard way to brush this off, by saying that QED perturbation expansion also only is asymptotic is very problematic, since in the QED case we are expanding around the perturbative vacuum state, so the asymptotic series may be useful. In string theory, the perturbative vacuum state is not what you want (you don’t want 10 flat-d gravity..), the choice of vacuum state is inherently a non-perturbative effect. And you don’t have a viable non-perturbative theory.
As Smolin explains, an accurate statement of the current situation is that, after many years of very difficult work, my colleague D.H. Phong and his collaborator (my fellow grad student Eric d’Hoker) managed to figure out how to properly define two loop superstring amplitudes and show that divergences cancel in this case. The way this works out is different than people had conjectured before the d’Hoker-Phong results. At higher loops the problem is even more difficult. Berkovits has very recent results using a different definition of the superstring, but as far as I know, his formulation has not yet led to the kind of understanding of higher-loop calculations that would allow you to say that they were definitely finite. While it certainly seems more than plausible that higher loop amplitudes will turn out to be finite, I don’t think characterizing the evidence for the finiteness of higher loop amplitudes as “extremely compelling” is in at all accurate. And, at best, finiteness applies to the terms, not to the sum, which is what one ultimately cares about.
As for whether the evidence for “gauge/gravity duality” is “extremely compelling”, it all depends on exactly what you mean by this. For certain things there is strong evidence, for others there is none. For example, in the full version of the duality the AdS superstring is supposed to be exactly dual to N=4 SSYM. But, see above, no one even knows how the define the AdS superstring non-perturbatively, so one doesn’t even know what the theory on that side of the duality is supposed to precisely be. A standard claim one hears is that in this case one should take N=4 SSYM as a non-perturbative definition of the superstring. If one does this, the evidence for what you want is then “extremely compelling”, but I don’t think that’s what you have in mind…
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But, see above, no one even knows how the define the AdS superstring non-perturbatively, so one doesn’t even know what the theory on that side of the duality is supposed to precisely be.
One can, however, do superstring perturbatively in the plane wave limit of the AdS background which allows a direct comparison that works out.
In my opinion, the problem with both string theory and loop quantum gravity is that they tend to a theory of everything.
Sean,
I don’t want to stray too far off topic, but I would like to respond to one part of Peter Woit’s comment. Most of the recent research on establishing the duality between N=4 SYM and strings in AdS_5 x S^5 focuses on the large N limit. This means that the string coupling is taken to zero, so the nonperturbative string effects that Peter worries about are not applicable. Presently, the problem on the string side is to solve a well defined field theory in two dimensions. Unfortunately this is not so easy, but people are trying.
In my opinion, the problem with both string theory and loop quantum gravity is that both sides are publically over-optimistic about grasping at straws, rather than to listen to guys like Roger Penrose.
Whatever it is that forces people to commit (fanatically?) to something that became so obviously absurd that even people like John Horgan can see it… only because he isn’t committed to defend either’s “belief” system.
http://arxiv.org/abs/hep-th/0401208
Dirac’s hole theory and quantum field theory are generally thought to be equivalent. In fact field theory can be derived from hole theory through the process of second quantization. However, it can be shown that problems worked in both theories yield different results.
To me the “debate” means that it’s “almost” time to back-up and “recapitualte”.
no, really, I kin spell that!
Joe,
The point of my comment to Sean was just to note that saying there is “extremely compelling” evidence for “gauge/gravity duality”, with the only remaining problem that things are not rigorously proven to mathematician’s standards is misleading. As you explain, it is only in certain limits that one has a handle on this duality, and even in those calculations are difficult and much remains to be understood. Mathematical rigor is not the problem.
Sean,
I respect your review of ‘Trouble..’ but you are a cosmologist by training, not a physicist. Smolin was already a well-established tenured physicist with lots of papers in string theory at the time of your graduation. Your reputation is served by keeping things honest, balanced, accurate, with a proper perspective of who is the senior fellow here. (I have absolutely no relationship with Smolin.)
That said, it is overdue that the String community, especially the high priests and their arrogent followers, get a kick in the butt. They are spending public money and have not been totally honest about results. Smolin is certainly NOT the problem, and should be congratulated.
What triggered the backlash are the devastating lack of scientific results from ST after some 25 years, the blatant attempts to excuse the failure by inventing the stupid Landscape and even tried to sell it to the public, the conspiracy to maintain high NSF funding by producing incomprehensible nonsense, and last but not least, by conducting hyped and fanciful pronouncements of the magic of ST in the public media. The public can be excused for thinking that ST researchers are in it for the money, that it has been taken for a ride. If ST pretends to be science, then it must produce clear scientific results.
The leadership of Strings will do well to get its act together before those who decides on NFS grants decide to do it for them.
I respect your review of ‘Trouble..’ but you are a cosmologist by training, not a physicist.
Boggle.
dark-matter. Just as a point of information, Sean is most certainly a physicist by training. I’m not quite sure what it would mean to be a theoretical cosmologist by training.
dark_matter wrote,
That’s pretty funny. Perhaps dark_matter is confusing cosmology with cosmetology.
I know how he feels, though. I have to keep reminding my doctor that he’s trained as an ophthalmologist, not as a physician.
Hi Sean,
Thanks for the nice review.
A friend pointed out that the issue might be the words “string theory”. If we simply said that everyone was doing foundational work on QFTs, then this would probably eliminate all concerns, and bring what the “string theorists” do squarely back into the fold of very very conventional (and uncontroversial) physics. Given the success of the SM, who could argue that a systematic study of QFT/gauge theories is not important?
2 thought experiments:
1) Suppose Riemann hadn’t invented RG, and Einstein’s wife hadn’t told him about it. Suppose instead that Einstien had, in addition to coming up with GR, also had to invent a big chunk of RG (maybe suppose Gauss also hadn’t proved his theorems in Diff Geo).
One can easily imagine Einstein and a cadre of young physicists and mathematicians taking a detour from the “conventional physics paradigm”, and working out the details of RG and its relationship to GR as a ten-year long aside. Isn’t this pretty obviously a fair analogy of what’s been going on in string theory, just more people and longer timescale (and of course, no guarantee of great success at the end)?
1a) When will physicists begin to appreciate the fact that string theory *must* be on to *something* when it’s extending our basic understanding of mathematics so much? If we still believe (as I think we all do) in “The Unreasonable Effectiveness of Mathematics in the Natural Sciences”, doesn’t the converse hold some water? That is, if string theory is having an unreasonable effectiveness in Math, then perhaps this is actually very good evidence that some science is around the corner…
2) Suppose it’d taken experimentalists decades to discover the anti-proton? How long before Dirac is considered a quack? When should we have started cutting off his research, for putting negative signs where they don’t make any sense (isn’t this as bad as “too many dimensions” or “too many notes”?). I know Smolin’s point is that “good” theories get verified quickly, but that could be as much an accident of the early-mid 20th century as anything else.
We spent thousands (even millions…) of years _not_ having enough experiments at hand to even think of a working theory – is it so bad that we’re spending a few decades working out a theory without having experiments?
‘Suppose it’d taken experimentalists decades to discover the anti-proton? How long before Dirac is considered a quack?’ – slow geezer
It did take 3 years to discover the positron, the first antimatter, and it was just as well. Dirac initially (1929-31) claimed that the anti-electron was the proton, which was already known. It was only a matter of months before Anderson discovered the positron (in 1932) that Dirac gave up trying to explain the mass discrepancy and was forced to accept that the anti-electron was not the proton but was an unobserved particle.
This prediction was his LAST RESORT. Dirac much preferred to be modelling existing phenomena and explaining existing data, than making speculative predictions. All solutions to a model must have a physical corrspondence in the real world. When you think about string, with 10^500 ground states giving that many variations of particle physics, it is kind of a nightmare version of Dirac’s problem.
First, there is no evidence that any of the solutions is the real standard model, and second, even if it is, you have no way of confirming that the other solutions are real (Susskind’s claim that all the solutions are real particle physics in parallel universes is just religion, uncheckable, unverifiable wishful thinking).
sigh.
it was crazy of me to plunge down this rathole in the first place, and crazier still for me to try and reply to your post. so it goes.
i think it’s safe to say that neither you nor I have have any idea how the landscape of CY’s is going to turn out; we don’t understand the first thing about Calabi-Yaus. We have proved some big theorems about 3-folds, but our understanding of them is about on par with 19th century understanding of surfaces.
There are many stupid questions about CY manifolds that we can’t begin to answer (like, could we even write down an actual CY metric?). Given that our understanding of these guys is so primitive, I think it’s silly to speculate at all about any of this.
If we didn’t know RG, we would still be in Euclidean axiom-land in our understanding of geometry. Continuing my thought experiment from above, it would be supremely silly to have discarded GR because it made no sense because the geometries violated Euclid. If string theory is true, we’ll undoubtedly ferret something out about CY mflds that’s as revolutionary as the Lobachevsky plane was.
The above argument would be unfair (i.e., could be used to justify anything), except that we’ve already had a few Lobachevsky-plane-level revolutions in mathematics that have been predicted by string theory. Recasting Morse theory, Atiyah-Singer, Donaldson theory via duality – that would be enough. But we also have Mirror Symmetry, Kontsevich’s insights into derived categories, and now Ed’s breaking new ground on Geometric Langlands. This is beyond a miracle, no?
And it’s not just hero-worship of Ed, hasn’t been for years. Kontsevich’s talk at ICM ’94, Okuonkov’s work, Givental, as well as that of dozens of other physicists and mathematicians. This is probably the most fruitful period of geometry since the 60s and Smale/Milnor/Thom/Bott/Atiyah.
I guess that’s what’s stunning to me. I agree that science is about experiments, but I also see that the math/physics distinction is an artificial boundary invented in the 20th century, one that didn’t apply (and couldn’t have applied) to Archimedes, Newton, Gauss, Fourier, to name a few physics revolutions. A boundary that we are rightly ignoring today, as we search as honestly as we can for the truth.
‘slow geezer’,
thanks awfully for your rigorous 😉 reply, especially the bits about this being a rat hole and your being crazy to try to reply to [a rat]. 😉
nc, these ratholes are terribly seductive, plus we’re all rats 🙂
Dear Sean
Thanks very much for an intelligent, perceptive review. If I may, then just a few words about the points where we disagree, because differences in judgment about these are at the heart of the issue.
1) Background independence. You assert, “It’s unclear whether this is really such a big deal. Most approaches to string theory are indeed background-dependent…but that’s presumably because we don’t understand the theory very well. This is an argument about style; in particular, how we should set about inventing new theories.”
No, this is not about style, it is about a necessary criteria a fundamental physical theory should satisfy. The argument for this goes back to Leibniz, and the literature is extensive. I won’t repeat what I said in the book and in papers such as hep-th/0507235. General relativity should, in the view of many experts have settled it on the side of background independence. For the many experts in physics and philosophy who are convinced of this, this is a non-negotiable criteria, which string theory so far does not satisfy. (For those who think it does, see below.) I believe the case for background independence is convincing and that many who are not convinced have simply not thought the issue through carefully enough.
There is a style issue but it is not about background independence, it is about two communities, one of which is familiar with the history of thought about the nature of space and time, the other of which is more pragmatic and feels they can “wing it” , use the same kinds of techniques that work in background dependent QFT to evaluate a quantum theory of gravity, and do not feel the need to make a careful study of the literature on the physical interpretation of GR before attempting to go beyond it.
As to whether the lack of background independence in string theory is, as you assert, “… because we don’t understand the theory very well,” this is a fond hope of mine, and it was the theme of my second book, Three Roads to Quantum Gravity. I spent many years trying to make a background independent approach to string theory-indeed LQG came out of this. So far it hasn’t convincingly worked, although I think that the direction I explored, which was a background independent membrane theory based on a matrix-Chern-Simons theory has promise. But being one of the few people to have tackled this problem, I should say it is not easy and I am worried that so few other people seem to be putting any effort into it.
It is sometimes asserted that AdS/CFT is a background independent formulation of string theory. This cannot be correct, because the whole point of background independence, going back to Leibniz’s principle of the identity of the indiscernible, is that there can be no global symmetries in a fundamental theory. This is true of GR with compact boundary conditions, and certainly not true of AdS/CFT which has a large group of global symmetries, What AdS/CFT doers show us is that a global internal symmetry can be dual to a global spacetime symmetry, but this is not background independence.
2) The need for rigorous mathematical foundations and proof for fundamental theories
You say:, “Both the finiteness of stringy scattering and the equivalence of gauge theory and gravity under Maldacena’s duality are supported by extremely compelling evidence, to the point where it has become extremely hard to see how they could fail to be true.”
Two issues are being confused here. First, there is not now a complete argument either for the finiteness of all orders string scattering or the strong form of the Maldacena conjecture, even at the theoretical physicists level of rigor. There are interesting developments in progress concerning finiteness, which is good, but nothing so far that is generally accepted at working to all orders. There is not even a closed form definition of “string theory on AdS^5 X S^5 backgrounds ” so there is not even a precise mathematical statement of the strong form of the Maldacena conjecture. And at no level of rigor is there a proposal for either the basic principles of string or M theory or the basic equations of the theory.
Second, it is just not the case that we never prove things in physics. There is only one area where this is true-and then only partly-which is QFT. It is true that the standard model is very successful experimentally in spite of the fact that there is a lot of theoretical evidence it cannot have a rigorous formulation. But this is not a good model for a fundamental theory, for we accept this situation by casting the standard model as an effective field theory. It is certainly OK to work with an effective field theory which has no rigorous formulation, but that is precisely because we have good evidence that it is to be replaced by a more fundamental theory. Indeed, the expectation that the standard model has no rigorous underpinnings is one of the arguments for the need for a unification beyond the standard model.
But a claim for a fundamental theory is something else, for it cannot-by definition-have a more fundamental underpinning. So it must stand up on its own. This means we must be able to formulate it cleanly and precisely and the important properties it enjoys should be theorems. It doesn’t mean physicists should all work at a rigorous level, but that rigorous framework must be there to refer to.
This is not an unrealizable ideal. Classical Newtonian mechanics satisfies it. So does classical statistical mechanics, ordinary non-relativisitic quantum mechanics and general relativity. In each of these cases there is a body of rigorous results and a community of mathematical physicists who work on them.
Is this too much to hope for theories of quantum gravity. No! LQG has a rigorous foundation, given by Ashtekar, Isham, Lewandowski, Thiemann and others. The central result in the whole subject of LQG is a rigorous theorem, the LOST theorem (math-ph/0407006, gr-qc/0504147). It asserts that there is a unique quantization of a diffeo invariant gauge theory with 2 or more spatial dimensions, subject to some technical, but physically reasonable conditions.
To respond directly to your quote above: given the apparent difficultly of proving the perturbative finiteness of superstring amplitudes, it is perfectly conceivable that it fails at some order. The delicate issues that make it hard to prove, such as those that concern the boundary of supermoduli space or the ambiguities of gauge fixing at arbitrary genus, are not to my knowledge addressed by power counting arguments that underlie our intuitions about when quantum field theories are perturbatively finite. My guess would be these problems can be overcome, but some mathematicians I now who have worked on these problems are not so sure. Even if it does, given how many QFT’s that are well behaved in perturbation theory fail to exist rigorously, and given that we have strong evidence that the string perturbation series is divergent, it is reasonable to worry that string perturbation theory, like the perturbation theory in QED, will not define a rigorous theory. And, as discuss in the detail in the book and in earlier papers (hep-th/0303185, hep-th/0106073), it is perfectly conceivable that a weaker form of the AdS/CFT conjecture is true, which does not rely on there being something rigorous corresponding to string theory on AdS/CFT.
I think that the difference between people who are and are not convinced by the evidence in these cases comes down to the following: do you have at the back of your mind the belief that there is a mathematical structure corresponding to the exact formulation of string theory? If you reason assuming that the answer is yes, you tend to be convinced that the conjectures we have been discussing are true. But if you do not reason that way, and take the existence of a mathematical structure corresponding to exact string theory as an open conjecture, yet to be decided, you find it more plausible that many partial results could be true about a structure in perturbation theory or weak coupling, and yet, as in the case with many QFT’s, no rigorous theory exists that they approximate.
3) LQG, You say that “general relativity is not well-behaved at short distances and high energies, where such new degrees of freedom are likely to play a crucial role” The LOST theorem just mentioned implies that GR, and indeed any diffeomorphism invariant gauge theory, is well defined at short distances. We understand in detail how spatial diffeomorphism invariance removes divergences from diffeo invariant quantum gauge field theories. We understand this in many different calculations, some rigorous, some not, some involving the behavior of operator products, some involving the behavior of path integrals. If you do not understand this you do not understand the basics of LQG. At this point the only thing to say is to ask you to please learn the basics of the subject before further commenting on it.
4) On why string theory so strongly dominates over other approaches. You say, “String theorists have somehow managed to convince all of these people that their field is worthy of support; I personally take the uncynical view that they have done so through obtaining interesting results.” To some extent this is certainly true. But some of those results generated expectations that have since been disappointed, with regard to uniqueness and the ability to generate predictions, as well as with regard to the existence of M theory, which is still a conjecture.
To some extent it may also be true that in the evaluation of the promise of string theory, departments took key conjectures as proven. As I describe in TTWP, some physicists I’ve spoken to in departments I’ve visited were unaware that perturbative finiteness, AdS/CFT and M theory were still open conjectures, without proof. Indeed, a few years ago, when I tried to find out what the precise situation was with regard to these conjectures, I had to ask many string theorists before finding someone who could give me the correct answer, so many experts were also confused and believed more was shown about these issues than has been.
One example of what I mean is the following: in many presentations M theory is presented as if it were something that already exists, rather than its true status which is a theory that has yet to be constructed. I personally think it is misleading to show the usual star diagram and say this is M theory: we know the boundaries but we don’t know much about the interior, when the correct thing to say is that dualities satisfied by the theories on the boundary support belief in a conjecture that there is a theory that fills in the whole space, but we do not know if that conjecture is true because we do not have a satisfactory candidate for this theory. Indeed, perhaps as a result of talks which were no precise about this, some non-string theorist physicists I’ve spoken with had the impression that there really is a well formulated theory by the name of M theory.
For what its worth, we in LQG were for the most part, very careful not to overclaim or exaggerate our results. If anything, the practice in non-string approaches to quantum gravity is to underclaim, as this is more the style in mathematics and in European science, where most workers come from. Indeed, I used to be sometimes an exception to this, and when I have on occasion over-claim my friends told me in harsh terms that it was harming the field.
You claim I over-hype certain results in LQG, but in the book I make it very clear that these are early, preliminary results and that much remains to be done before we can see if their promise is realized.
Does this difference in styles have anything to do with the relative success in gaining positions, funding etc in the US? I don’t know, but I think it is a question worth asking. In fact there has been much substantial progress in non-string quantum gravity and quantum gravity phenomenology over the last ten years. If you are right, should we be starting to see some interest in hiring the people responsible for them?
5) On the connections with experiment. Of course evidence for extra dimensions or supersymmetry would provide moral support for string theory, but they would not provide confirmation for string theory itself. Neither do they contradict LQG, which can accommodate them. But the key point here is that the Planck scale is accessible through astrophysical measurements and those experiments are ongoing. The question that is experimentally accessible is whether Poincare invariance is broken or deformed at the Planck scale, if it is experiment will over the next few years detect this. This is important to stress because so many of us-including me-used to argue that the Planck scale is inaccessible. Consequently, there is a growing activity of Planck scale phenomenology, which is so far not very appreciated in the US.
Finally, I am glad we agree about the need to do things to encourage more intellectual independence within US Science. But then you say ” In the real world, it’s difficult to see what to do about the problem.” No, there are a number of things we can do and I have made some obvious suggestions in my book and in my Physics Today essay. The first step is to talk with people like venture capitalists and investment fund managers about how they succeed in diversifying investments in a climate of scarce resources. Some of the obvious proposals I discussed were already implemented by the founders of PI such as making sure to hire people working on more than one approach to a fundamental problem. Others have been implemented by the FQXi foundation, which is to target people whose work takes big professional risks to attack foundational problems and fund them. More could be done both by departments and by foundations such as NSF, by simply changing the questions asked during peer review so as to give more advantage to people inventing and carrying out their own research programs and disadvantaging people doing unimaginative and unambitious “me-too” science.
But let me close by again thanking you for a perceptive review.
Lee