The Trouble With Physics

By Sean Carroll | October 3, 2006 12:02 am

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.

CATEGORIZED UNDER: Science, Words
  • Josh

    Right on.

  • Aaron Bergman

    3000 words. Feh. That’s nothing….

  • http://blogs.discovermagazine.com/cosmicvariance/sean/ Sean

    Aaron, of course, reviewed Not Even Wrong at extraordinary length.

    http://golem.ph.utexas.edu/string/archives/000898.html

  • http://catdynamics.blogspot.com Steinn Sigurdsson

    Is the gauge/gravity duality formally proven, or does it remain an intuitively obvious plausible conjecture?

  • http://www.valdostamuseum.org/hamsmith/ Tony Smith

    Sean, thanks for a very “fair and balanced” review (my apologies for using a Fox News phrase, but in your case I think that it really does in fact apply).

    You say “… The abstract argument – about academic culture and the need to nurture speculative ideas – is … important and largely correct …
    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 …”.

    In an iinterview at http://www.ipm.ac.ir/IPM/news/connes-interview.pdf , Alain Connes said:

    “… From my point of view the actual system in the US really discourages people who are truly original thinkers … I believe that the most successful systems so far were these big institutes in the Soviet union, like the Landau institute, the Steklov institute, etc. Money did not play any role there, the job was just to talk about science.

    the way the young people … in the US … get their position on the market creates “feudalities” namely a few fields well implanted in key universities which reproduce themselves leaving no room for new fields. … Beginners have little choice but to find an adviser that is sociologically well implanted … so that at a later stage he or she will be able to write the relevant recommendation letters and get a position for the student … all these letters look alike in their emphatic style. The result is that there are very few subjects which are emphasized and keep producing students and of course this does not create the right conditions for new fields to emerge. …”.

    Could USA universities do what Connes suggests and copy what Connes perceives to be the useful aspects of the Soviet institutes, that is,
    create a lot of low-paying but secure research-only jobs (NOT teaching-slave-jobs), with no pressure to produce papers, thus allowing really motivated people to survive while doing whatever theoretical high-energy physics they want to do for as long as they want to do it, in an environment with good library-internet facilities and a community of like-minded others with whom they can interact, by discussion, seminars, etc., if they choose to do so ?

    Maybe the vast majority of such subsistence researchers might produce very little of note, but it would allow a Grisha Perelman type person to survive while doing work they love, and if even a very few of them make very big breakthroughs, the advances might be significant.

    Tony Smith
    http://www.valdostamuseum.org/hamsmith/

  • fh

    I’m about to start my PhD in variants of Loop Quantum Gravity. You argue that young PhD students simply do what convinces them. To a degree that’s true, but in my case it was only through my curious reading around and some intuition that I found out about LQG. What convinced me more then anything was the difference in style you mentioned.

    However, within my University in Munich there simply would have been nobody to tell me about any other approach then String Theory. And that’s the one of the biggest faculties for Physics in Germany.

    And LQG has some remarkable results to show, however, these do not stand in the tradition of particle theory, there are no scattering amplitudes, in fact the very issue of precisely defining scattering amplitudes took over a decade. This further deepens the “cultural divide”.

    Regarding the “hype” of particles in the fabric of spacetime, these results are real, though to different degrees. Some structures of the Standard Modell do show up here and there but it’s far from clear that these behave approximately like QFT particles on a background metric in an appropriate limit. On the other hand connections between Spinfoam models and QFT have been discovered as well.

    LQG is far smaller and younger then String theory, whether or not we are heading towards a first revolution the next few years will show. However, with respect to background independence it is important to note that String theorists have come around to the point of view that it’s crucially important, that string theory in it’s background independent form implies radically new structures of space and time. Background independence means that the very concept of “short scale behaviour of gravity” makes no sense.

  • fh

    Let me just extend on what I said regarding SpinFoams and QFT, it is becoming increasingly clear that SFs are a genuine generalization of background spacetime QFT. But these are results from right now, as opposed to the decade old Malcadena conjecture. Furthermore it’s not coming in the form of a grand conjecture but much more gradually. I think part of what Smolin is doing is simply telling people what has been achieved so they can take a look and make a judgement.

  • jianying

    The next revolution in physics will probably be when the duality between LQG and string theory is discovered. And the two warring camps can come together and realize that the only way to make progress is by helping each other.

  • fh

    jianying

    people are looking at that, but while it makes for a nice narrative, it’s far from guaranteed. One or both theories might just as well turn out to be wrong.

  • bart Licovski

    Gravity is a wave not a particle, Structures in space time are no more equivelent to judgment than to the Tao . Gravity is stuctured by other influences of gravity space and time reorganizes due to gravitation thus gravity and quantum loop feedbake can be equel after space time is adjusted back to itself after the a particular gravity well made in mass by gravity. It is ok to say we know electromagnetism can influence matter in unbeilievalble ways its just like yin and yang of tao. Is mass a function of a gravity well that can be moved in space and time in the universe on the linear scale also? just something to think about

  • Thomas Dent

    Nobel Prize goes to Mather and Smoot for COBE … not a very controversial choice.

    http://www.dn.se/DNet/jsp/polopoly.jsp?d=2567&a=576448&previousRenderType=6

    concludes Guth and Linde are still in for a long wait.

  • http://www.chrononaut.org/~dm/ David Moles

    fh wrote:

    Background independence means that the very concept of “short scale behaviour of gravity” makes no sense.

    fh, can you expand on that? It sounds like you’re implying that background independence does away with scale entirely — I would have thought scale would still exist as a concept, just not as an absolute. (But I’m not a physicist or a mathematician, so….)

  • http://eskesthai.blogspot.com/2006/10/cp-violation.html Plato

    Brian Greene:

    The goal of ISCAP is to bring together theoretical physicists, astrophysicists, and observational astronomers to address key problems in particle physics and cosmology that require a broad confluence of expertise and perspective.

    I think leaders in both camps are really trying to “tie up” loose ends:) And must stop thinking of “each other” as Angels and Demons:)

    To think Lee may of cut off his right arm, is a sad “state of affairs?”

    To think gravity as extended versions tested in society,”time clocks and such” one couldn’t help but wonder about such “conceptual changes” housing new perspective.

    Okay, it’s far distant from the theory of GR, but heck, moving it to the quantum region, makes it no less important?

    Good review Sean, and to the others you have mentioned.

  • http://snews.bnl.gov/popsci/contents.html Blake Stacey

    I’m just waiting for the day when some bright grad student, after making the coffee-shop round in Amsterdam, returns to prove that LQG is actually some esoteric limiting case of M-theory.

  • fh

    I may have overstated there. It’s a trivial observation really, in a theory without a backround spacetime, that is, with diffeomorphism invariance, correlators do not depend on distances. Diffeos take W(x,y) to W(f(x),f(y)) so W(x,y) is really quite independent of x and y. In a relational picture you break diffeo invariance by thinking about matter degrees of freedom that fix locations and paths in the gravitational field.

  • Markk

    Reading the book as a person with a B.S. in physics who went on into Engineering and whose only connection to Physics departments now is to go to Alumni events and get asked for money, I think you are correct halfway in how the book struck me. The half about the sociological issues facing High Energy Physics jumped out at me also. The part about LQG I think you are seeing from the inside. I didn’t read any real big arguements for LQG in this book, other than the fact it is there along with some other theries about alternate relativity rules and reformulated algebraic models. Aside from the last none of the others seemed to me to be any more convincing than String Theory.

    I tell you this, this book would make me think twice about donating to my alma mater’s Physics department if it was heavily into String Theory or whatever it is called. What got to me was the numbers of people. It sounds like there are hundreds of people (perhaps thousands over the last 20 years) who have or are working on String Theory. Given those enormous resources, I would expect that “guage/gravity” duality would have been pinned down within 5 years, that many other simplifications would have been made. Since they have not it seems like String theory has the Mongolian Horde problem common in big projects. Less people might be more effective since it is obviously not in the last ditch effort area yet.

  • http://quasar9.blogspot.com/ Quasar9

    Hi Sean, I take it all that flowed spontaneously.
    An excellent review composed of a stream of unbiased and uncynical comments on string theory ans string theorists.

    Blake, esoteric? doesn’t QG impose ‘constraints’ on M-Theory? Esoteric or exotic from Amsterdam, maybe closed (loop) strings are LQG

  • http://sophronismos.blogspot.com/ Dave

    Thanks for this review, Sean. I have a morbid curiosity about these issues, despite being a non-scientist, and your analysis was interesting. I will note my surprise at the shadow of Thomas Kuhn that appeared in the review and the comments. I was under the impression that Kuhn’s understanding of scientific truth was somewhat discredited among scientists.

  • http://blogs.discovermagazine.com/cosmicvariance/sean/ Sean

    Steinn, gauge/gravity duality is not “formally proven,” but there is overwhelming evidence for it. You check things over and over and they keep matching. There is always the possibility that we are being fooled, but I don’t think so.

  • Thomas Larsson

    Diffeos take W(x,y) to W(f(x),f(y)) so W(x,y) is really quite independent of x and y.

    One needs to be careful here. The correlation function

    W(x,y) ~ |x-y|^-2h.

    is clearly not diffeomorphism invariant. However, it is diff invariant to claim that W(x,y) asymptotically has this form when x and y approach each other. In particular, the anomalous dimension h is diff invariant. The underlying reason is that the dilatation operator D = x^u d/dx^u is independent of the metric.

    Note also that a conformal transformation in 2D is the same thing as a diffeomorphism in one complex dimension, but infinite conformal symmetry in 2D is nevertheless compatible with correlators of the form W(z,w) ~ (z-w)^-2h.

  • fh

    The point of the argument is precisely that the correlators can not have the form W(x,y) ~ |x-y|^-2h if diffeos are a symmetry that is implemented unitarily in a straightforward naive way.

    I can’t speak on the 2D case I haven’t looked much at conformal symmetries and string theory, sorry.

  • Thomas Larsson

    However, it can be possible if infinite-dimensional symmetries are implemented unitarily in a not-so-straightforward way, namely with an anomaly. A non-zero h requires a conformal anomaly, which changes the conformal algebra to the Virasoro algebra. Now guess who discovered the Virasoro-like extension of the diffeomorphism algebra in higher dimensions :-)

  • http://blogs.discovermagazine.com/cosmicvariance/sean/ Sean

    I appreciate the discussion, but please let’s not use this thread to hash out technical points about diffeomorphism invariance…

  • http://deferentialgeometry.org/ Garrett

    Heh, just as described by Sean’s review, the comments have two threads going at once. I’d like to chime in and thank Tony for providing the quote from Connes in comment 5, as well as say I liked his proposal for the establishment of… what to call them… “theory hostels”? Connes’ insight is particularly compelling since he is one of few researchers to have come up with a viable TOE independent of strings and LQG.

  • strategichamlet

    Sean,

    In the past you have criticized scientists for being ignorant of philosophy, especially for making statements about philosophy without formal training. Whenever you discuss String Theory, however, you seem to take a distinctively positivist attitude. Now from at least the 20th century philosophers I’ve read, positivism is the only philosophy universally hated by them all. One could argue that they doth protest too much since after all if positivism is a good way to go, why would we need philosophers? That being said there are plenty of good critiques of positivism.
    Basically, I’m curious how you square your views on scientists and philosophy with your views on String Theory which seem to simplify to: String Theory deserves it’s virtually monolithic position in theoretical physics because when most scienists look at it they think it’s the best bet.

  • my one cent

    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.

  • Charon

    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.

  • http://blogs.discovermagazine.com/cosmicvariance/sean/ Sean

    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?

  • http://christinedantas.blogspot.com/2006/09/interesting-links.html nc

    ‘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

  • http://blogs.discovermagazine.com/cosmicvariance/sean/ Sean

    nc, I am pretty sure that the prediction of gravity is not likely to be contradicted by experiment.

  • http://christinedantas.blogspot.com/2006/09/interesting-links.html nc

    Ho ho, ha ha …

  • Pingback: Not Even Wrong » Blog Archive » Controversy, Controversy….

  • http://www.math.columbia.edu/~woit/wordpress Peter Woit

    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…

  • http://nothingnow didouwolf

    hi.Sean
    sorry u dont know me , just bu chance look your thinks here .
    imm,nothing , maybe we never recognize ,
    but i want write somthing here cos after i did read all your words.
    u know , i m sad now , i doubt everthing now ,i come cross i think is real love but later .i found .its a love begining from a lie. i m shocked.i dont now what to do and i search “techanicle of lie” in google. so i did got here.”… it involves less techanicle points but contain the most insightful view on the deep meaning of quantum mechanics. … Okok, it’sa Lie bracket but still, it makes formulas ugly. And then there is the infamous appendix on what a great …”
    this letter of you lead me come here.nothing , forgive a stranger .
    nice know you.

  • Aaron Bergman

    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.

  • adam

    In my opinion, the problem with both string theory and loop quantum gravity is that they tend to a theory of everything.

  • Joe Minahan

    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.

  • http://www.anthropic-principle.ORG island

    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”.

  • http://www.anthropic-principle.ORG island

    no, really, I kin spell that!

  • http://www.math.columbia.edu/~woit/wordpress Peter Woit

    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.

  • dark-matter

    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.

  • Aaron Bergman

    I respect your review of ‘Trouble..’ but you are a cosmologist by training, not a physicist.

    Boggle.

  • http://blogs.discovermagazine.com/cosmicvariance/mark/ Mark

    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.

  • Belizean

    dark_matter wrote,

    but you [Sean] are a cosmologist by training, not a physicist.

    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.

  • slow geezer

    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?

  • http://electrogravity.blogspot.com/2006/10/nature-reviews-dr-woits-book-not-even.html nc

    ‘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).

  • slow geezer

    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.

  • http://electrogravity.blogspot.com/2006/10/nature-reviews-dr-woits-book-not-even.html nc

    ‘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]. ;-)

  • slow geezer

    nc, these ratholes are terribly seductive, plus we’re all rats :)

  • Lee Smolin

    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

  • http://blogs.discovermagazine.com/cosmicvariance/sean/ Sean

    Lee–

    Thanks for the response. Briefly:

    1) You misunderstood what I was saying about background independence; perhaps I was not clear. Parenthetically, it is certainly not the case that quantum gravity must necessarily be background-independent; I could easily imagine, for example, a set of overlapping descriptions in different regimes, each of which referred to some background, but when taken as a whole described the entire theory. (Tom Banks has discussed ideas along these lines.)

    But that’s not what I was talking about. The “style” I referred to was the style of developing new theories, not what the theories looked like. Whether or not we someday find a background-independent formulation of quantum gravity, that has nothing to do with some imaginary requirement that we will only make progress toward that goal by insisting on background-independence from the start. Perhaps we will get there eventually, as we eventually got to quantum mechanics through Bohr’s quantization rules and so on. I just don’t know; but since nobody else does either, at the moment it’s simply a guess, which different people are welcome to have.

    2) We’ll just have to disagree about the rigorous-results issue. Of course I never claimed that it is or would be impossible to prove things rigorously, only that we can make substantial progress without doing so (for example, in every realistic quantum field theory).

    3) My claim was not that quantum GR is non-unique or ill-defined, it was that it is ill-behaved. These are not the same thing; I know plenty of people, for example, who exist and are unique and well-defined yet very ill-behaved. There is no reason to think that gravity has an ultraviolet fixed point or some other nice behavior, and there is every reason to believe that non-gravitational degrees of freedom will play a crucial role in understanding the behavior of gravity at short distances. Jacques spelled all of this out very clearly in his posts:

    http://golem.ph.utexas.edu/~distler/blog/archives/000612.html
    http://golem.ph.utexas.edu/~distler/blog/archives/000639.html

    and I haven’t seen anyone even attempt to answer his questions.

    The swipe at my understanding of the subject was gratuitous; let’s stick to substantive arguments, shall we? It’s true that I haven’t gone through the details of the proof of the LOST theorem, so I can’t judge how general its hypotheses really are, or what the implications of the result might be in detail. But the claim is that there is a unique representation of the “kinematical algebra.” I don’t see how this has much bearing on the issue at hand, which is about dynamics, not kinematics. How does having a unique representation help you derive the low-energy effective theory, for example?

    4) Again, I think we’ll just have to disagree. In my personal experience, the reason why more jobs have not been allocated to people working in non-stringy approaches to quantum gravity is not because those people are too modest and careful about stating their results.

    5) Of course it would be interesting and exciting to get experimental data relevant to the Planck scale, and of course things like extra dimensions are not a unique signature of string theory. As I said in the review, in both string theory and other approaches, we have ideas for experimental results that would be compatible with the theory, but no firm predictions that would falsify it if they were not found. Does LQG make a prediction about ultra-high-energy cosmic rays that, if data from Auger were inconsistent with the prediction, would rule out the theory once and for all?

  • Aaron Bergman

    Hi Lee –

    Can you list some people who believe that string theory will not eventually be background independent (modulo boundary issues)? You go on radio programs talking about these deep philosophical differences going back hundreds of years, and as best I can tell, they don’t exist. We’ve all read MTW, and some of us have even read Hawking and Ellis. Why do you continually place yourself in the role of the defender of Einstein when none of us are attacking him?

    What there is, as Sean states, is a difference of approaches, but that hardly is indicative of this grand historical context that you seem so fond of.

    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.

    It’s good to know that background independence is still a moving target, though.

    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.

    As far as I can tell, it does not do any such thing. The LOST theorem discusses a particular representation of a particular algebra before the imposition of all the constraints. The physical aspect of the theory is the Hilbert space with all the constraints imposed and, as best I’ve been able to discern, the LOST theorem has little to say about that.

    Don’t you think we should be careful about `hyping’ our results?

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  • http://golem.ph.utexas.edu/~distler/blog/ Jacques Distler

    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.

    I’m afraid I don’t understand this statement.

    In a noncompact space one only mods out by diffeomorphisms that go to the identity at infinity. In asymptotically flat spacetimes, this means that Poincaré acts a global symmetry of the gravitational theory.

    And bona fide observables (e.g., the ADM energy) transform as nontrivial representations of Poincaré.

    Similarly, in asymptotically AdS space, there is a group of global symmetries, and bona fide observables transform in nontrivial representations of that symmetry group.

    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.

    And, therefore, it is true in any theory containing quantum field theory as a systematic approximation. Which is to say, it is true of any theory of “fundamental physics” that we might possibly be interested in.

    First, there is not now a complete argument either for the finiteness of all orders string scattering

    There seems to be a tremendous amount of confusion (if not outright misinformation) about the status of that subject. See here for a discussion of what is (and is not) known.

    … or the strong form of the Maldacena conjecture

    Berenstein, Maldacena and Nastase (and their successors) showed that the duality holds well beyond the supergravity approximation. That, and the myriad of other checks, makes it hard to see how any weaker form of the conjecture could hold, but not the strong form.

    Do you have a proposal for some weaker form of the conjecture that is actually consistent with all the currently-known evidence?

    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.

    There is no example of a sensible nontrivial quantum field theory, defined by its perturbation theory. So there is no reason to expect that string theory will either. If it were, then string theory would be dead in the water. So it’s rather a good thin that its perturbation series is not convergent.

    We’ve spent the past decade learning tantalizing things about aspects of nonperturbative string theory. It’s rather like the blind men and the elephant., but what we do know about string theory is far more interesting that what one learns from string perturbation theory alone..

  • http://blogs.discovermagazine.com/cosmicvariance/clifford/ Clifford

    Hi Lee,

    We’re all waiting to read your response to Jacques’ Jeff’s question over on Asymptotia. You asked for members of the community to respond directly to your book’s contents, and he’s done so – asking again the question about why you seem to have downplayed the role of research which tries to apply string theory to the strong interactions in a book that criticises the program of research in string theory for not being relevant to experiment.

    We’re all very curious to read your answer.

    Best,

    -cvj

  • http://golem.ph.utexas.edu/~distler/blog/ Jacques Distler

    We’re all waiting to read your response to Jacques’ question over on Asymptotia.

    I believe you mean Jeff’s question. While I might appreciate being mistaken for Jeff Harvey, I’m not sure he would be so thrilled.

  • http://blogs.discovermagazine.com/cosmicvariance/clifford/ Clifford

    Whoops! Will correct…. Short term memory shot to pieces so that I forget thing while moving between two browser windows. Thanks.

    -cvj

  • Thomas Larsson

    Hi, Lee.

    If you are interested in background independence in 4D, why not start by looking at background independence on the circle, where diffeomorphisms are well understood? There the situation is like this:

    1. There is a unique theory with c = 0, namely the trivial one.
    2. There are many unitary theories with c > 0.

    As I pointed out above, the notion of an anomalous dimension is background independent, since the dilaton operator does not involve the metric. Therefore, you should find the same anomalous dimensions with and without a background metric.

  • Jeff Harvey

    Dear Lee,

    I’d be interested in your answer to my question on Clifford’s
    blog as well. Since you want feedback and I don’t have the time to collect all my questions and responses in one place, I’ll ask another question here.

    One of your main criticisms of string theory involves the possible landscape
    of solutions to string theory. For example, in the introduction, on page xiv,
    you have a paragraph that starts with “Part of the reason string theory
    makes no new predictions is that it appears to come in an infinite number
    of versions.” and ends with “No experiment will ever be able to prove it true.”
    There are many other places in the text where you focus on this point as
    one of the central flaws of string theory.

    I have two responses. The first, which I mentioned on the radio show, is
    that the existence of an infinite number of solutions does not at all
    imply a lack of predictions or falsifiability. QFTs are infinite in number, but
    once you make a choice of QFT (gauge group, representation of matter
    fields, values of masses and couplings) you can make definite dynamical
    predictions which of course in the Standard Model have been tested rather
    precisely. There is no reason that string theory could not have similar
    features. In fact, there seem to be certain fairly universal results in string
    theory. These include the computability of black hole entropy in a wide
    variety of backgrounds and the universality of the viscosity to entropy
    ration in the QGP. I agree with you that the landscape (if it exists) is
    problematic for the initially hoped for prediction of parameters of the Standard
    Model, but this is not the only conceivable way of testing string theory.

    My second response is really a question to you. You end your discussion
    of the Landscape in Chapter 10 with a statement of your own point of view
    on the problem. You say “If you insist on those standards, then you will not
    believe in the vast number of new theories, because the evidence for any theory in the current landscape is pretty minimal according to the old standards. This is the point of view I find myself leaning toward, most of
    the time. It just seems to me the most rational reading of the evidence.”
    My question: Why do you criticize string theory for having a property that you don’t believe it has, at least most of the time?

  • Moshe

    If I may, let me amend Jeff’s question with my own – how large is the space of all background-independent quantum field theories, do we have a reason to believe it is not infinite?

  • http://eskesthai.blogspot.com/2006/10/extracting-beauty-from-chaos.html Plato

    While the issue with Lee Smolin is being cleared up, I thought it important that people read KC’s article for themself and think about what has manifested in the comment section supplied in regards to “The Tea CUP,” as well as Peter Woit’s Corrections post.


    The claim that string theory can’t be tested is serious; experiment is the ultimate arbiter of truth. But it’s impossible to know what is ultimately testable. When the ghostly neutrino popped up in one of Pauli’s equations, the physicist admitted he’d done “a terrible thing. I have postulated a particle that cannot be detected.” Then in 1956, traces of neutrinos were seen in the wash of radiation spewing from newly commissioned nuclear reactors.

    As a lay person as I watched the debate. I learned of what is important to science people. This was a lesson for me, and I hope one the public will appreciate.

  • Lee Smolin

    Hi,

    Thanks for the different questions and responses. If I may, I’ll quickly answer a few now and come back to others that require more thought later.

    To Jeff, First, thanks for taking the time to do the radio show.

    “Why do you criticize string theory for having a property that you don’t believe it has, at least most of the time?”

    This is a fair point. If we don’t accept the KKLT and related flux vacua, there are then two possibilities: 1) There are no non-supersymmetric consistent string perturbation theories, and 2) There are consistent non-supersymmetric string perturbation theories yet to be found.

    If 1) is true then there may be a problem incorporating the observed dark energy in string theory altogether. This would be one way to disconfirm string theory. Alternatively, to show that 2) is true we should find a new way to construct non-supersymmetric string theories.

    I certainly don’t know which of the three possibilities is right, I hope people are working on both alternatives to the KKLT etc landscape.

    To Moshe:, “how large is the space of all background-independent quantum field theories, do we have a reason to believe it is not infinite?” I don’t think we know. At the Hamiltonian level it is pretty hard to get the gravity parts of the quantum constraints to close, but once they do it seems possible to add different forms of matter and maintain that property. At the spin foam level we don’t have good control on the space of possible amplitudes or of RG flow through them, I have been urging people to work more on this for a long time; perhaps due to the few number of people involved, most have been concentrating on first understanding the properties of Barrett-Crane and related models.

    There is of course the new possibility found in recent work of Markopoulou and Krebs that shows that a large set of pure quantum gravity models have additional conserved quantities and local excitations that carry them. These are naturally interpreted as particles, and their properties should be computable with no additional parameters. But we have a long way to go to understand if the dynamics comes out right, even if there are preliminary indications that something like a preon model comes out.

    Dear Sean, with regard to LOST: “I don’t see how this has much bearing on the issue at hand, which is about dynamics, not kinematics.” The point is that the theory is then unique (for a fixed value of the cosmological constant) also at the spatially diffeomorphism invariant level, because the unique kinematical representation carries a rep of the spatial diffeo group and this lets one construct rigorously and explicitly the Hilbert space of spatially diffeo invariant states. One can then argue that any operator product in the kinematical Hilbert space that is defined re the limit of a regularization procedure, such that it gives rise to a well defined operator on the Hilbert space of diffeomorphism invariant states, has no uv divergences. This is confirmed in many calculations and results.

    So the existence of the Ashtekar-Lewandowski representation (of the kinematical algebra) allows us to construct a Hilbert space of spatially diffeo invariant states on which the hamiltonian constraint and other operators are represented by uv finite operators. This is pretty important, it is how uv finiteness is shown. Then the LOST theorem tells us that this construction is unique.

    Now this may or may not prevent there from being some space of parameters that govern possible consistent Hamiltonian constraint operators. But it does appears that matter content is not tightly restricted by uv finiteness, because of Thiemann et al’s results that the consistency of the quantum constraints on this Hilbert space is not altered by adding different matter fields and couplings.

    This is, so far as I can tell, a proof that quantum general relativity a) exists and is uv finite and b) does so with a variety of fundamental matter couplings or with no matter at all. These results then, directly contradict your assertion: “There is no reason to think that gravity has an ultraviolet fixed point or some other nice behavior, and there is every reason to believe that non-gravitational degrees of freedom will play a crucial role in understanding the behavior of gravity at short distances.”

    So we have a genuine disagreement. It seems to me that either you have to concede you are wrong or find an error in the LOST theorem or related results.

    To be completely clear, one possibility is still that the Hamiltonian formulation these results refer to do not have a low energy limit that reproduces classical GR. We have several indications that this is so, but so far no proof, so on present results it is still possible that while quantum GR exists as these results show it does not have GR as a low energy limit (i.e just as quantum YM theory does not have classical YM’s theory as a low energy limit.) Indeed, it may be that only the path integral form of the theory captured in spin foam models has GR as a low energy limit. So there is not yet a claim that LQG passes all the tests for a good quantum theory of gravity. But there is the claim that at both the Hamiltonian and path integral levels there is a well defined theory which corresponds to the quantization of GR that is well defined and uv finite, which contradicts your assertions.

    Thanks,

    Lee

  • Moshe

    Thanks Lee, my point is of course that is that if and when LQG will make contact with low energy effective field theory, all indications are that it will have its own landscape to deal with.

    I have to say the discussion regarding tachyons in non-SUSY vacua (in Clifford’s space) sounds awfully familiar, maybe someone else will have something more convincing to say.

    Finally, congratulations! hope you are getting a bit of sleep already.

  • Thomas Larsson

    So we have a genuine disagreement. It seems to me that either you have to concede you are wrong or find an error in the LOST theorem or related results

    It is also possible that the LOST theorem is correct but that some assumption (e.g. no diff anomalies) is not realized in nature.

  • http://electrogravity.blogspot.com nc

    Dear Plato,

    The neutrino wasn’t a non-testable prediction but a FACT from experimental data on beta decay spectra.

    Experiments show that beta particles, which are the most common decay mechanism in the chart of nuclides, have a continuous spectrum of energies (unlike gamma rays, which are line spectra, indicating that they occur from quantum-type energy state transitions in the nucleus).

    The beta spectrum curve does have an upper limit however, and the mean energy of the beta particles is around 30% of the upper limit.

    The data indicated that the mean energy emitted by the beta particles was far less than the total energy lost per beta decay. There are only two ways of accounting for this: (1) abandon law of conservation of energy (which Niels Bohr wanted to do, or at least make that law subject to statistical indeterminancy and wishy-washyness) or (2) postulate a new particle.

    Pauli decided to write down all the charcateristics he could about the postulated new particle. Using conservation of angular momentum and other laws, Pauli was able to predict the spin and other characteristics of neutrinos. He wanted to call it the neutron, but Chadwick stole that name for another particle, so Pauli settled on the neutrino name.

    FINALLY, Pauli DID say it was possible to TEST the neutrino theory:

    http://www.math.columbia.edu/~woit/wordpress/?p=389#comment-10746

    Wolfgang Pauli’s letter of Dec 4, 1930 to a meeting of beta radiation specialists in Tubingen:

    ‘Dear Radioactive Ladies and Gentlemen, I have hit upon a desperate remedy regarding … the continous beta-spectrum … I admit that my way out may seem rather improbable a priori … Nevertheless, if you don’t play you can’t win … Therefore, Dear Radioactives, test and judge.’

    (Quoted in footnote of page 12, http://arxiv.org/abs/hep-ph/0204104 )

    All it took to test was a strong source of neutrinos. It is telling that Enrico Fermi, who worked out the original theory of beta decay, also invented the nuclear reactor, which was used to discover the neutrino ;-)

    Best,
    nc

  • http://arunsmusings.blogspot.com Arun

    LQG, if successful, would have the relationship to General Relativity that QED has to classical electromagnetism. How would a landscape arise?

  • Moshe

    Arun, loop “quantization” is an attempt to generalize QFT in a way that preserves backround-independence explicitely. The attempts so far are to reproduce pure gravity (and if I may add, quantum mechanics), but as Lee emphasizes one can do the same thing to gravity coupled to any form of matter, with any dynamics and any couplings, and so far there seems to be no difference. So the number of low energy universes coming from the theory is apriori infinite, unless one finds some “selection principle”, or more pessimistically the number ends up being zero.

  • http://electrogravity.blogspot.com nc

    Moshe, LQG is a modelling process, not a speculation. Smolin et al. show that a path integral is a summing over the full set of interaction graphs in a Penrose spin network. The result gives general relativity without a metric (ie, background independent). Next, you simply have to make gravity consistent completely with standard model-type Yang-Mills QFT dynamics to get predictions (cf comment#29).

  • http://blogs.discovermagazine.com/cosmicvariance/sean/ Sean

    Lee– I don’t have time right now for anything but a quick response, but to my mind the fact that you have a Hilbert space and some Hamiltonian, but don’t know whether the theory recovers GR (or some close relative thereof) in the classical limit, is not a minor technicality. It’s basically the whole point. To me, “quantum GR” does not mean “a diffeomorphism-invariant representation on Hilbert space”, it means “a quantum-mechanical theory that reduces to GR in the classical limit.”

    In particular, again, I don’t see how the model answers “Georgi’s objection” discussed in Jacques’s posts linked to above. String theory has an answer, and I think that any competitor should as well.

  • Aaron Bergman

    They don’t have a definite Hamiltonian last I checked. I could be wrong on this point, though.

  • http://arunsmusings.blogspot.com Arun

    Moshe:

    Does classical general relativity have a landscape problem? After all, one can put any kind of matter with any dynamics and coupling into it. I do not expect LQG to any more constrain matter than GR does. The fact that LQG or GR does not constrain matter is not the landscape problem that string theory has. The string theory landscape problem as I understand it is that the degrees of freedom are supposedly exactly known (at least at high energy) but can manifest themselves in the low energy limit in myriads of inequivalent ways.

    If LQG works, then the theory of (not everything, but everything we know about) will be LQG + the Standard Model. If we discover something know at LHC, the theory will be LQG + the Standard Model + LHC extensions. And so on. No landscape problem here.

    Of course, “Georgi’s objections” make it unlikely that LQG will work. Perhaps even more than finding a classical limit, this objection needs to be addressed (in my highly inexpert opinion).

    -Arun

  • http://arunsmusings.blogspot.com Arun

    Question to Sean: does the gravitation theory that emerges in the “classical limit” of string theory have the principle of equivalence, or is there plenty of low energy matter that doesn’t?

  • http://blogs.discovermagazine.com/cosmicvariance/sean/ Sean

    Arun, all of ordinary physics — e.g., classical or quantum field theory — has a “landscape problem,” in that there are a gajillion (really, an infinite number of) possible models. It used to be thought that we would distinguish between them by doing experiments, which makes sense to me. Of course it would be great if there were some profound principle that picked one out as unique, but the absence of such a principle doesn’t seem like such a disaster to me.

    In modern parlance, “violating the principle of equivalence” just means “having some new long-range forces of approximately gravitational strength.” String theory could have such forces (the dilaton is an obvious candidate), but it’s not necessary, as the forces would be undetectable if their associated fields were given a relatively large mass.

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  • Lee Smolin

    Dear Sean, Jacques and others,

    It seems to me we have answered Georgi’s objection over and over again. I’ll try it again. First, is this the complete statement of it (from http://golem.ph.utexas.edu/~distler/blog/archives/000639.html): “The point is that there’s no decoupling regime in which quantum “pure gravity” effects are important, while other particle interactions can be neglected. “Universality” in field theory — usually our friend — is, here, our enemy. Unless we know all particle physics interactions all the way from accessible energy up to the Planck scale, we can never hope to extract any quantitative predictions about quantum gravitational effects.”

    This is true unless there is a universal mechanism that cuts off quantum gravitational fluctuations and the fluctuations of anything else, because as a consequence of this mechanism there are simply no degrees of freedom with wavelength smaller than the Planck length. In fact, there is a such a mechanism, and it is understood, as I said, both heuristically and rigorously. To understand it heuristically you have to think carefully about how imposing spatial diffeomorphism invariance limits what can come out of an operator product, regulated through a point splitting procedure.

    This is clearly described in the literature now for more than 10 years, please read the literature at whatever of rigor you are happy with. Then come back and either indicate you agree or indicate that there is a technical error somewhere in the proofs of this.

    This implies that the uv problem does not suffice to fix the matter couplings. This however does not imply that the theory can make no predictions. An example is 2+1 gravity with matter as solved by Freidel and Livine. A universal effect is a deformation of the Poincare symmetry governed by a single computable parameter. If this turns out to be true also in 3+1, as indicated by semiclassical calculations, it implies predictions for GLAST.

    Please tell me why this does not answer Georgi’s objection.

    Also, to Sean, “whether the theory recovers GR (or some close relative thereof) in the classical limit, is not a minor technicality. It’s basically the whole point…” Certainly, and therefore you should be celebrating with us the results of Rovelli et al that show that the graviton propagator emerges from a spin foam path integral with the correct low energy behavior, demonstrating that the theory has gravitons and also a Newtonian gravitational force. You should also be celebrating with us the Freidel-Livine results I just mentioned as they show that in this interacting, perturbatively non-renormalizable model (2+1 gravity coupled to matter fields) the low energy limit emerges and it is QFT in a background spacetime, but on a non-commutative manifold.

    These are important developments, but they were not the first indications that LQG has a good low energy limit. There were also various results showing that there are semiclassical states which approximate classical metrics and that QFT on background manifolds emerges as an approximation when one studies excitations of those states.

    And while I agree with your sentiment, it didn’t have to turn out that the quantization of GR does give a rigorously defined hilbert space and observables algebra, but it did. Shouldn’t this be a clue? The fact that we now have good evidence that the low energy limit has gravitons is then I would think compelling.

    Thanks,

    Lee

  • http://golem.ph.utexas.edu/~distler/blog/ Jacques Distler

    This is true unless there is a universal mechanism that cuts off quantum gravitational fluctuations and the fluctuations of anything else…

    No!

    This is true, unless there is a universal mechanism that cuts off quantum fluctuations of everything else except gravity. Then, and only then, would we have a regime where quantum gravity effects were important, but where the effects of other interactions were negligible.

    Georgi’s assertion is that there is no such mechanism.

    Is the nature of his objection clear, now?

  • nc

    Dear Jacques, that is really, really funny! ;-) But even if LQG in present form is wrong, that is far better than being not even wrong. At least an error of omission can be corrected, simply by supplying a necessary mechanism. ;-)

  • Lee Smolin

    Dear Jacques,

    The key sentence in your assertion is “Unless we know all particle physics interactions all the way from accessible energy up to the Planck scale, we can never hope to extract any quantitative predictions about quantum gravitational effects.” I gave you an explicit example, in the work of Freidel and Livine, in a solvable (but perturbatively non-renormalizable) model, which contradicts that assertion because the global symmetry of the ground state is deformed in a way that leads to “quantitative predictions.”

    If you examine the actual calculation you can see how this works. They define a scattering amplitude in terms of a spin foam model. This gives a sum over diagrams. These can be organized in terms of matter Feynman diagrams. For each matter Feynman diagrams one has to sum over the degrees of freedom of the gravitational field. These are topological degrees of freedom in the 3d spacetime mod the Feynman diagram. This sum can be done for each diagram, and the effect is a universal deformation of the Feynman diagrams corresponding to a quantum deformation of Poincare symmetry.

    It seems to me this is a counterexample to your claim above,

    Thanks,

    Lee

  • http://countiblis.blogspot.com Count Iblis

    How would we know that there is no new physics hidden beyond the Planck scale? Suppose that LQG or string theory can be made to work, all you have is a consistent theory of quantum gravity.

    Suppose we could go back in time and educate ancient Greek Mathematicians about Classical Mechanics, Special and General Realitivity, and Classical Electrodynamics. Then sooner or later they would have found out that there are inconsistencies in elctrodynamics when you attempt to take into account the back reaction of emitted radiation in a fully consistent way.

    But I doubt that they would have been able to invent quantum mechanics as the correct solution without doing experiments.

  • http://golem.ph.utexas.edu/~distler/blog/ Jacques Distler

    Unless we know all particle physics interactions all the way from accessible energy up to the Planck scale, we can never hope to extract any quantitative predictions about quantum gravitational effects.” I gave you an explicit example, in the work of Freidel and Livine, in a solvable (but perturbatively non-renormalizable) model, which contradicts that assertion.

    You wish to quibble with the word “any” ? OK …

    I am well-familiar with the work of Freidel and Livine, and I draw exactly the opposite conclusion from it.

    In 2+1 dimensions, there is no local dynamics in the gravitational field. Ergo, the rationale for Georgi’s complaint: that there is no way to disentangle the effects of quantum gravitational dynamics from the effects of other (a-priori unknown to the low-energy observer) fields.

    In 2+1 dimensions, there’s simply nothing to disentangle. And, indeed, Freidel and Livine show that the gravitational degrees of freedom can be integrated out once and for all (in closed form!), yielding a noncommutative effective field theory for the matter fields.

    In 3+1 dimensions, there is local dynamics in the gravitational field, and so Georgi’s objection comes into play.

    Obviously, attempting to emulate Freidel and Livine in 3+1 dimensions is doomed to failure. The gravitational field has local propagating massless degrees of freedom. Integrating out gravity would yields an intractable, hopelesly nonlocal mess.

    This is already clear at the semiclassical level, which is why I was puzzled by your previous comment:

    If this turns out to be true also in 3+1, as indicated by semiclassical calculations, it implies predictions for GLAST.

    I would love to believe you that LQG actually makes testable predictions for GLAST. But I don’t. And, if GLAST returns a negative result, I suspect that we will hear that neither do you.

    Anyway, if you feel that the word “any” in the above statement of Georgi’s objection is too strong, I’d be happy amending it to something less categorical.

    But the spirit of his objection still holds..

  • http://philadelphia.craigslist.org dumbstringtheoritician

    sorry to most people who’re really devoted to making serous comments about a pop science book, with all my respect.

    here are just some funny stuff I couldn’t fail to notice about one post from LQG theorist Dr. Smolin:
    “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”
    :D :D It seems to me that the “a few words” are a lota words, more than a whole window on the Safari browser takes.

    consequently ” the points where we disagree” is just about everything.

    As dumb as I am, I have a side in the pick. Also hopefully you smart and serious guys out there don’t get confused between the functions of pop science and real science.

    If asked the question which of the two (or one) theories are apparently more relevant to the real world, I wouldn’t hesitate a second to say it’s definitely string theory. and you guys who don’t know field theory well enough and criticize string theory for being irrelevant should really think twice before saying that again.

    but there’s no proof LQG is ruled out. I can certainly agree to the statement that there’s a chance it’s a good theory for something, even maybe gravity of some worlds.

    from the communist camp, we were told that philosophy that matters are extracted from things that happen :) obviously that’s not how the world outside that camp (which one existed) think. so I really agree a significant number of string theorists should dirty their hands now, as the LHC is at least in principle quite related to what many string theorists are doing, while (sadly) it cannot be said about the LQG at the present stage.

    I think Peter Woit should start criticizing LQG too, only to be fair to “not even wrong” theories by his standard.

  • https://nige.wordpress.com nc

    Regards the physics of the metric: in 1949 some kind of crystal-like Dirac sea was shown to mimic the SR contraction and mass-energy variation, see C.F. Frank, ‘On the equations of motion of crystal dislocations’, Proceedings of the Physical Society of London, A62, pp 131-4:

    ‘It is shown that when a Burgers screw dislocation [in a crystal] moves with velocity v it suffers a longitudinal contraction by the factor (1 – v^2 /c^2)^1/2, where c is the velocity of transverse sound. The total energy of the moving dislocation is given by the formula E = E(o)/(1 – v^2 / c^2)^1/2, where E(o) is the potential energy of the dislocation at rest.’

    Specifying that the distance/time ratio = c (constant velocity of light), then tells you that the time dilation factor is identical to the distance contraction factor.

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  • Advanced Extraterrestrial Being

    LOL!!!!

    You’ll never believe what the correct theory is! Unfortunately, I am unable to publish it.

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  • local

    what are your five unsolved problems?

  • http://www.zenmeister.de Frank Zimmermann

    I think most of the people commenting here and in fact the reviewer himself missed the point.

    The review itself and some comments also express the craftmens view on this book (there is no argue for string theory _or_ loop).

    For my opinion Lees objectives were different ones:

    I think he took string theory as a current example for doing science the wrong way.

    I agree with him totally that the current physics community is a kind of church and I think too that no relevant theory was born after the 1930ies. Thats a result of the dominating craftsmen in the physics community.

    Frank.

  • MoveOn

    @dumbstringtheoritician:

    “I think Peter Woit should start criticizing LQG too, only to be fair to “not even wrong” theories by his standard.”

    I guess he won’t. A while ago some of his readers had the brilliant
    idea of setting up a FAQ on his site. Great, I thought, let’s start
    with proposing some questions, and came up with:
    “What is the most overhyped theory of quantum gravity?”

    He immediately deleted my post. I guess because he knew the answer ….

  • http://nige.wordpress.com nigel cook

    MoveOn, Dr Woit deletes most comments people make unless they are attacks on him.

    LQG is explained in his book Not Even Wrong where he points out that loops are a perfectly logical and self-consistent duality of the curvature of spacetime: ‘In loop quantum gravity, the basic idea is to use the standard methods of quantum theory, but to change the choice of fundamental variables that one is working with. It is well known among mathematicians that an alternative to thinking about geometry in terms of curvature fields at each point in a space is to instead think about the holonomy [whole rule] around loops in the space.’

    LQG has the benefits of unifying Standard Model (Yang-Mills) quantum field theory with the verified non-landscape end of general relativity (curvature) without making a host of uncheckable extradimensional speculations. It is more economical with hype than string theory because the physical basis may be found in the Yang-Mills picture of exchange radiation. Fermions (non-integer spin particles) in the standard model don’t have intrinsic masses (masses vary with velocity for example), but their masses are due to their association with massive bosons having integer spin. Exchange of gauge boson radiations between these massive bosons gives the loops of LQG. If string theorists had any rationality they would take such facts as at least a serious alternative to string!

    Dr Woit’s focus isn’t a complaint about the failure of string to accomplish checkable physics but is a complaint about the continuing hype and the underhanded attacking by string theorists at alternatives in general despite the hypocrisy that this involves! He makes it clear that he does not see string theory as wrong, only that so far it has only produced hype, hype, hype, plus extra loud hype when someone complains about alternatives being unheard.

    Of course, he might see things from quite a different perspective if he was censored from posting papers to arXiv.org and so on. As it is, he can delete my embittered comments about string damaging physics as being mere noise.

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Cosmic Variance

Random samplings from a universe of ideas.

About Sean Carroll

Sean Carroll is a Senior Research Associate in the Department of Physics at the California Institute of Technology. His research interests include theoretical aspects of cosmology, field theory, and gravitation. His most recent book is The Particle at the End of the Universe, about the Large Hadron Collider and the search for the Higgs boson. Here are some of his favorite blog posts, home page, and email: carroll [at] cosmicvariance.com .

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