Science or Sociology?

Joseph Polchinski, 5/20/07

This is a continuation of the on-line discussion between Lee Smolin and myself, which began with my review of his book and has now continued with his response. A copy of this exchange (without the associated comment threads) is here.

Dear Lee,

Thank you for your recent response to my review. It will certainly be helpful in clarifying the issues. Let me start with your wish that I do more to address the broader issues in your book. When I accepted the offer to review these two books, I made two resolutions. The first was to stick to the physics, because this is our ultimate goal, and because it is an area where I can contribute expertise. Also, keeping my first resolution would help me to keep the second, which was to stay positive. I am happy that my review has been well-received. Your response raises some issues of physics, and these are the most interesting things to discuss, but I will also address some of the broader issues you raise, including the process of physics, ethics, and the question in the title. Let me emphasize that I have no desire to criticize you personally, but in order to present my point of view I must take serious issue both with your facts and with the way that they are presented.

Regarding your points:

**The fictitious prediction of a non-positive cosmological constant.** This is a key point in your book, and the explanation that you now give makes no logical sense. In your book you say (A) “*… it [a non-positive cosmological constant] was widely understood to be a consequence of string theory.*” You now justify this by the argument that a non-positive cosmological constant is a consequence of unbroken supersymmetry (true), so A would follow from (B) *Unbroken supersymmetry was widely understood to be a consequence of string theory.* But even if this were true, it would not support your story about the observation of the dark energy leading to a “genuine crisis, … a clear disagreement between observation and a prediction of string theory.” There would *already* have been a crisis, since supersymmetry must obviously be broken in nature; seeing the dark energy would not add to this. But in fact the true situation, as you can find in my book or in many review articles, was closer to the opposite of B than to B: (B’) *Supersymmetry is broken in almost all Calabi-Yau vacua of heterotic string theory. We have no controlled examples because at least one modulus rolls off, usually to a regime where we cannot calculate. The solution to this problem may have to wait until we have a non-perturbative formulation of gravity, or even a solution to the cosmological constant problem.*

In your response you largely raise issues surrounding B’, including the Witten quote, but I want to return to what you have actually written in your book. It is a compelling story, which leads into your discussion of “a group of experts doing what they can to save a cherished theory in the face of data that seem to contradict it.” It surely made a big impression on every reader; it was mentioned in several blogs, and in Peter Shor’s Amazon review. And it never happened. It is an example of something that that happens all too often in your book: you have a story that you believe, or want to believe, and you ignore the facts.

You go on to challenge the ethics of string theorists in regard to how they presented the issue of moduli stabilization in their talks and papers. I am quite sure that in every colloquium that I gave I said something that could be summarized as “We do not understand the vacuum in string theory. The cosmological constant problem is telling us that there is something that we do not understand about our own vacuum. And, we do not know the underlying principle of string theory. These various problems may be related.” The cosmological constant and the nature of string theory seemed much more critical than the moduli stabilization problem, and these are certainly what I and most other string theorists emphasized.

This *scientific* judgment has largely been borne out in time. In 1995-98 these incredible new nonperturbative tools were developed, and over the next few years many string theorists worked on the problem of applying them to less and less supersymmetric situations, culminating in the construction of stabilized vacua. Obviously many questions remain, and these are widely and openly debated. It seems like a successful scientific process: people knew what the important problems were, worked in various directions (a fair number did work on moduli stabilization over the years), and when the right tools became available the problem was solved. As you point out, the stabilization problem is nearly one hundred years old, and now string theorists (primarily the younger generation, I might add) have solved it. You are portraying a crisis where there is actually a major success, and you are creating an ethical issue where there is none.

*AdS/CFT duality.* You raise the issue of the existence of the gauge theory. There are two points here. First, Wilson’s construction of quantum field theory has been used successfully for 40 years. It is used in a controlled way by condensed matter physicists, lattice gauge theorists, constructive quantum field theorists, and many others. To argue that a technique that is so well understood does not apply to the case at hand, the scientific ethic requires that you do more than just say Not proven! Sociology! as you have done. You need to give an argument, ideally pointing to a calculation that one could do, or at least discuss, in which one would get the wrong answer.

I have given a specific argument why we are well within the domain of applicability of Wilson: there are 1+1 and 2+1 dimensional versions of AdS/CFT, which are also constructions of quantum gravity, and for which the gauge theory is super-renormalizable (and there are no chiral fermions): the counterterms needed to reach the supersymmetric continuum limit can be calculated in closed form – thus there is an algorithmic definition of the gauge theory side of the duality. You could perhaps argue that there will be a breaking of supersymmetry that will survive in the continuum limit, and we could sit down and do the calculation. But I know what this answer is, because I have done this kind of calculation many times (it is basically just dimensional analysis). Similar calculations, for rotational invariance and chiral symmetry, are routine in lattice gauge theory.

As a further ethical point, in your book you state that it is astounding that Gary Horowitz and I ignore the question of the existence of the gauge theory, and you then use this to make a point about groupthink (this is in your chapter on *sociology*). While you were writing your book, you and I discussed the above points in detail, so you knew that we had not ignored the issue but had thought about it deeply. You do not even acknowledge the existence of a scientific counterargument to your statement, and in saying that Gary and I ignore the issue you are omitting facts that are known to you in order to turn an issue of science into one of sociology. Again you impose your own beliefs on the facts; thus I am reluctant to accept as accurate the various statements that you attribute elsewhere to anonymous string theorists and others.

You raise again the issue of a weak form of Maldacena duality. As you know, it is very difficult to find a sensible weak form that is consistent with all the evidence and yet not the strong form. In my review I have gone through your book and papers and identified three proposals, and explained why each is wrong. Again, you have not acknowledged the existence of scientific counterarguments, but have just reasserted your original point. If your arguments had been made in a serious way, I would expect that you would have given some deep thought to them and be ready to defend them.

There are some interesting points, one of which I will turn to next.

**The role of rigor and calculation.** Here we disagree. Let me give some arguments in support of my point of view. A nice example is provided by your paper *`The Maldacena conjecture and Rehren duality’* with Arnsdorf, hep-th/0106073.

You argue that strong forms of the Maldacena duality are ruled out because Rehren duality implies that the bulk causal structure is always the fixed causal structure of AdS_5, and so there cannot be gravitational bending of light. But this would in turn imply that there cannot be refraction in the CFT, because the causal structure in the bulk projects to the boundary: null geodesics that travel from boundary to boundary, through the AdS_5 bulk, connect points that lie on null boundary geodesics. Now, the gauge theory certainly does have refraction: there are interactions, so in any state of finite density the speed of propagation will be less than 1. (Since Rehren duality does not refer to the value of the coupling, this argument would hold even at weak coupling, where the refraction can be calculated explicitly.)

You have emphasized that Rehren duality is rigorous, so apparently the problem is that you have assumed that it implies more than it does. Generally, rigorous results have very specific assumptions and very precise consequences. In physics, which is a process of discovery, this can make them worse than useless, since one tends to assume that their assumptions, and their implications, are broader than they actually are. Further, as this example shows, a chain of reasoning is only as strong as its weakest step. Rigor generally makes the strongest steps stronger still – to prove something it is necessary to understand the physics very well first – and so it is often not the critical point where the most effort should be applied. Your paper illustrates another problem with rigor: it is hard to get it right. If one makes one error the whole thing breaks, whereas a good physical argument is more robust. Thus, your paper gives the appearance of rigor, yet reaches a conclusion that is physically nonsensical.

This question of calculation deserves further discussion, and your paper with Arnsdorf makes for an interesting case study, in comparison with mine with Susskind and Toumbas, hep-th/9903228. (I apologize for picking so much on this one paper, but it really does address many of the points at issue, and it is central to the discussion of AdS/CFT in your various reviews.) You argue that there are two difficulties with AdS/CFT: that strong forms of it are inconsistent with the bending of light by gravitational fields, and that the evidence supports a weaker relation that you call conformal induction. We also present two apparent paradoxes: that the duality seems to require acausal behavior, and negative energy densities, in the CFT. The papers differ in that yours contains a handful of very short equations, while ours contains several detailed calculations. What we do is to translate our argument from the imprecise language of words to the precise language of equations.

We then find that the amount of negative energy that must be `borrowed’ is exactly consistent with earlier bounds of Ford and Roman, gr-qc/9901074, and that a simple quantum mechanical model shows that an apparent acausality in the classical variables is in fact fully causal when one looks at the full quantum state. Along the way we learn something interesting about how AdS/CFT works.

This process of translation of an idea from words to calculation will be familiar to any theoretical physicist. It is often the hardest part of a problem, and the point where the greatest creativity enters. Many word-ideas die quickly at this point, or are transmuted or sharpened. Had you applied it to your word-ideas, you would probably have quickly recognized their falsehood. Further, over-reliance on the imprecise language of words is surely correlated with the tendency to confuse scientific arguments with sociological ones.

Finally, I have recently attended a number of talks by leading workers in LQG, at a KITP workshop and the April APS meeting. I am quite certain that the standard of rigor was not higher than in string theory or other areas of physics. In fact, there were quite a number of uncontrolled approximations. This is not necessarily bad – I will also use such approximations when this is all that is available – but it is not rigor. So your insistence on rigor does not actually describe how science is done even in your own field.

**Background independence.** I think people are a bit tired of the who-is-more-background-independent argument, since it seems to come down to definitions. Let me put things in physical terms. As you say, suppose that the strong form of Maldacena duality is true. This would mean that we can consider a box as large as we want – a light-year, 10^{6} light-years, with an arbitrarily small negative cosmological constant, and AdS/CFT provides a complete construction of quantum gravity within that space. This would include: the formation and decay of (nonsupersymmetric) black holes; graviton scattering at hyper-Planckian energies; physically continuous transitions from one topology, through a quantum state with no geometric interpretation, to a different topology; states where a submanifold of spacetime has a noncommutative geometry; states with a variety of apparent geometric singularities, where the physics is nonsingular. All of these, and many others with a variety of geometries and topologies (you can put a lot in an AdS box), and arbitrary quantum superpositions of them, can be identified in the gauge theory, and so are described algorithmically by the duality. It may not include spaces with interesting cosmologies, or with an effective positive cosmological constant. You call this a very weak and limited form of background independence.

Even here you are blowing things out of proportion: your reply refers five times to the “global symmetry algebra,” but almost immediately after the original work of Maldacena, the duality was extended to systems with reduced symmetry, or none. Your own PI colleagues, Alex Buchel and Rob Myers, have made important contributions to this subject, and I note also the series of papers by Hertog and Horowitz on strongly time-dependent boundary conditions.

A second physics point concerns the constraints. It is not that I am ignorant of the conventional wisdom here, I am challenging it. You believe that the large Hilbert space in which the constraints act is necessary in order to describe all possible backgrounds of quantum gravity. No, only the much smaller set of states that satisfy the constraints is needed. The larger space may play a useful auxiliary role, but it is not physical: the universe cannot be in such a state, and observables must keep the system within the physical subspace. So what are these larger spaces for? One thing we have learned, from emergent gauge theory, is that they are not necessary: one can start from a system with no constraints, only physical variables, and the constraints are needed only to describe the classical limit efficiently. We have learned a similar lesson from dualities such as AdS/CFT: these larger spaces are very different in different classical limits, they are not intrinsic to the quantum theory. Thus, all this focus on constraints is putting effort into something that is unphysical and actually intrinsic to a certain classical limit.

**Cosmology**. I have agreed that we may be far from sharp prediction. However, string theory has played a valuable role in suggesting new ideas. Moreover, the variety of kinds of models being explored phenomenologically is large; it is clear that some of these arise easily in the landscape (e.g. a pure cosmological constant), while others may be rigorously excluded (the constraints of Arkani-Hamed et al, and others).

Regarding the atomic analogy, the long period that I was referring to was the hundred years between the first scientific argument for atoms (Dalton) and the confirmation (Brownian motion). I agree, however, that one should not get too caught up in analogies. No analogy is perfect: in the 19th century there was a wealth of unexplained phenomena from the natural world, while our current era is historically exceptional in that phenomena beyond the Standard Model are so few.

**RHIC.** You say that quantum gravity is not being used here. But the QCD plasma entropy is being related to the Bekenstein-Hawking entropy, which depends on hbar, and the ideal viscosity (a concept discovered through AdS/CFT, which is now a standard idea in heavy ion physics) is quantum mechanical.

Moreover, I am puzzled by your repeated statement that the evidence supports AdS/CFT describing only classical supergravity. The gauge theory is fully quantum mechanical, so if it contains classical gravity why is this not **exactly** what we are all looking for: a theory that unites Einstein’s theory and quantum mechanics? This should be of great interest to anyone working on quantum gravity – how does the gauge theory manage to do this? So we look closer, and we find that it’s… string theory! It is clear why you have trouble with this: according to your book, gravity is a theory of principle, which must be understood by seers, while gauge theory is a constructive theory, which can be built by craftsmen. AdS/CFT would then imply that craftsmen are dual to seers.

But seriously, duality does erase distinctions that we make with our classical experiences and vocabularies, because one quantum theory has many classical limits. Thus, quantum mechanics first erased the distinction between particles and waves. QFT dualities erased the distinction between quanta and solitons, which once seemed absolute. Maldacena duality erases at least much of the distinction between gauge theory and gravity. Unexpected perhaps, but those who ignore this lesson are likely to end up as backward-seers rather than forward-seers.

**Other physics.** Sean has suggested that I comment on the understanding of string theory in time-dependent backgrounds. Here I will give my own way of thinking about this, which is rather particle-physicsy; other string theorists might emphasize different things. If you have the flat spacetime S-matrix, you actually know a lot about curved spacetime, since you can form a very complicated geometry by throwing together a lot of gravitons in a coherent state. From a particle physics perspective, where the goal is to measure the underlying Lagrangian, this is enough: the S-matrix encodes all local physics in curved spacetime. Further, with this effective Lagrangian one can study processes in a fully curved spacetime, as long as the curvature stays below the string scale. One can then list things that are not covered by this: first, cosmological questions like initial conditions and spacetime singularities, and these are indeed open questions and the subject of active research; second, the possibility of an intrinsic non-locality in physics, so that local measurements do not capture everything. The second possibility has been widely discussed: the black hole information paradox gives a strong indication that such nonlocality exists; the black hole complementarity principle, and the holographic principle, are general statements of the nature of the nonlocality; and, the BFSS matrix theory and AdS/CFT duality are very concrete realizations of locality emerging from a nonlocal starting point. Certainly deep questions about the nature of time remain, and I expect that the solutions will build on our current understanding of the holographic principle.

On the UV finiteness of string perturbation theory, the one-line physics proof is that the regions of world-sheet moduli space that would correspond to UV divergences in field theory actually turn out to describe IR physics. The decomposition of moduli space that Zwiebach uses to formulate closed-string field theory is probably the best for seeing this. The IR divergences are described by low energy effective field theory, so the finiteness problem is reduced to the already-solved problem of IR divergences in quantum field theory. This may seem awfully simple, but I have done enough calculational checks of different parts of it to take it seriously.

**Ethics and sociology.** Coming back to ethics, the principal scientific ethic is that scientists take responsibility for what they say: When a statement is made, to what extent has it been thought through, and appropriate checks and counterarguments considered (and, yes, the appropriate calculations done)? To what extent are known difficulties acknowledged? When a new counterargument is given, is it addressed, and the original assertion modified if necessary? Are facts presented in a clear and direct manner? This is howscientists judge one another. It is clear why this is necessary: science works by the parallel activity of many minds, and it is necessary that information be exchanged in as accurate a way as possible. Given the above discussion, I find your claim to the ethical high ground to be ironic.

Regarding group-think: you interpret the reaction of string theorists to your book as more evidence for your point of view. Rather, I think that much of this is a natural reaction to what many see as a distorted presentation of the facts. Regarding the personal insults, I think that you set the tone here with characterizations such as that quoted in the *New Yorker*, so it seems like posturing for you to claim the high road when a few string theorists respond in kind. However, I hope that those contributing to this discussion will try to keep to the same reasoned attitude that I have tried for.

Overwhelmingly the concentration on string theory is a scientific judgement, made by a very diverse group of theorists. Look at any of the several dozen most well-known string theorists: my own scientific experiences and tastes, both inside and outside string theory, are very different from any of theirs, just as they are from each other. I think of myself as a theoretical physicist first, and cross over the boundaries between string theory and several other fields depending on what looks important and interesting, as do many others. String theorists can be rather focussed, but they are not as closed to new ideas as you portray. For example, such ideas as holography and eternal inflation were developed outside of string theory, and might have become `alternative ideas.’ Instead they were recognized as likely parts of the big picture.

There is a reasonable concern that younger string theorists, educated in string theory rather than in other fields, might find it harder to cross these lines. Indeed, during the first and second string revolutions, there was inevitably more concentration, as these new ideas opened up a whole range of new concepts and methods. It is a very positive development that new connections between string theory and other areas have developed – heavy ion physics, low energy hadronic physics, LHC physics, cosmology, mathematics, general relativity, and many areas of quantum field theory – and that many young people are taking advantage of the opportunity to cross these lines, and in both directions. This broadening of perspective should be, and I think is, strongly encouraged.

Coming back to the question in the title, I have agreed that sociological effects exist; they must, since science is a human activity. However, when I read your book, knowing the facts, the case actually seems quite weak. To make the case for a strong sociological effect, at each turn you are forced to stretch the facts beyond recognition. On the other hand, when you discuss the science, your overemphasis on the usefulness and applicability of rigor ignores the kind of physical reasoning that physicists actually use in practice with great success, so your are leaving out at least 95% of what makes physics really work.

That’s an awful lot to read. Could you maybe summarize it in lolcat form? Say, “Im in ur moduli space, describin ur IR divurgensez.”

If there is a more interesting discussion underway anywhere on the planet, I’m certainly not privy to it. I am very pleased that this debate is public and appreciate the effort being made on both sides to keep things civil.

It seems to me that the non-scientific parts of this debate, relating to sociology or epistemology, are reaching the end of their useful lifecycle, becoming (as such things tend to do) an essentially semantic debate with quickly diminishing returns. The specific scientific points, however, are becoming more interesting with each iteration of the argument.

Thanks to you and Dr. Smolin for your efforts and to the Cosmic Variance owners for all their work.

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Professor Polchinski

Thank you for taking the time to work through, and address scientifically, the arguments and allegations in Smolin’s book. I am sure that this is not what you would prefer to be doing with your time, but leaving these claims unaddressed would result in public misunderstanding of the status of modern theoretical physics, and risk long term damage to the field.

Again, thank you for your time and effort.

Thanks, Professor Polchinski.

I think, everybody with in interest in the status of modern theoretical physics (certainly me) really appreciates the public sientific debate on Smolin’s book.

The Trouble with Physicsdoes list some trivial issues with the claims of string theory, so I’m not surprised to see Professor Polchinski, author of a major work on string, take issue with these points.I would like to just ask: “what, if anything, would make string theorists finally concede that completely non-string alternative ideas should be objectively compared to string theory?”

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Nigel on May 21st, 2007 at 5:35 pm

asks:

“I would like to just ask: “what, if anything, would make string theorists finally concede that completely non-string alternative ideas should be objectively compared to string theory?” ”

I am not a string theorist so I can’t speak for “string theorists”. However, as a working particle theorist I can say that it has *always* been standard practice that *all* alternative ideas should be compared not only to string theory but also to each other, and more importantly to whatever data we can bring to bear on them. I have personally worked on models of technicolour, compositeness, supersymmetry, susy-GUTS, non-commutative geometry (a la Connes, and a la deformation quantization), and string theory: I’ve also worked on the physics of black holes and on cosmology but that’s not relevant here [incidentally most working particle theorists that I know have a range of research interests at least as large as mine] . Some of these classes of models have been slain by data, others have hit a wall in terms of our ability to develop and understand them, and some have survived and thrived. That’s science! Physics is always bustling with novel theories, and ideas for their confrontation with experiment. All theories must show their (calculational) goods, and live up to the scrutiny of experiment and the comparison to other theoretical alternatives. So what you’re asking about is the normal practice of physics and goes on all the time.

I think that that was by far the most effective rebuttal of Prof Smolin’s book I have seen, and it goes some way towards cancelling the effects of the writings of you-know-who.

The weakest point, however, is the discussion of the cosmological constant. I think that there is no denying that [a] the discovery of a positive CC was not expected by string theorists, and came to many of them as a very unpleasant shock, that [b] had the CC turned out to be negative, the temptation to claim this as a triumph for string theory would have been irresistible, and [c] to claim that the moduli stabilization problem has been “solved” is a bit over the top.

I’d like to step back and ask: what non-string alternative ideas

arethere that are being seriously considered to explain what the Standard Model doesn’t explain (which, I assume, is primarily having gravity finally get along with everybody else)?And what is the moduli stabilization problem? (There’s no relevant wikipedia article! I’m lost!)

mollishka, when you compactify all those extra dimensions, there are various parameters that tell you the size and shape of the compactification. These show up as scalar fields in the four-dimensional world; the earliest example was good old Kaluza-Klein theory, where the radius of the compact circle leads to a scalar field now often called the “radion” or “dilaton.” More generally, the scalars are known as “moduli.”

But these moduli usually have potentials, and they usually tend to not have minima, or at least not in a perturbative regime where you can calculate anything. Instead, they get pushed off to infinity, which is inconsistent with the world we observe. So we want to stabilize the moduli, which turns out not to be so easy. Various new ideas (of which Joe was one of the pioneers) involving combinations of warping, fluxes, branes, and instantons seem to show that it can be done. (Perhaps an expert can be more explicit than that.)

“Various new ideas (of which Joe was one of the pioneers) involving combinations of warping, fluxes, branes, and instantons seem to show that it can be done. (Perhaps an expert can be more explicit than that.)”

It seems highly fine tunned to me. Fluxes, branes, warping and instantons? it might as well be a bunch of angels. I am sure there is a vacuum where some little turtles do the job π

I dunno, it looks like without experimental guidance (like Joe points out we live, unfortunately/fortunately, in a highly successful period with lilttle new physics out there to crank some calculations for) this whole discussion is just pure sociology. Of course we can appeal to the rigor of mathematics, but at the end of the day we want to understand nature not just play around with symbols, even though we all admit is fun. Polchinski is right in clarifying missleading argumentations, and after all this is about Smolin’s book and his claims and not the failure of String Theory (ST) to provide any experimental confirmation. I agree all what is has been developed under the ST tag is pretty amazing and worthwhile exploring given its potential usefulness in other areas of physics. The ADS/CFT correspondency is remarkable, even though from an EFT point of view isnt that incredible. Perhaps the best achievement is to relate a non-gravitational theory to a theory with gravity, that is cool. The other way around is also quite interesting, even though alcohol is quite different than water, we all kinda know this already, dont we? π

Noboru Nakanishi and Izumi Ojima have written a sceintific masterpiece called “Covariant Operator Formalism of Gauge Theories and Quantum Gravity”. It is therefore most interesting to read what these authors have to say about the superstring paradigm and related issues. Here’s what I found (highly recommended, deep and spiced with a lot of humor…)

<em> http://www.math.columbia.edu/~woit/nakanishi1.pdf </em>

<em> http://www.math.columbia.edu/~woit/nakanishi2.pdf </em>

<em> http://www.math.columbia.edu/~woit/nakanishi3.pdf </em>

<em> http://arxiv.org/abs/hep-th/0610090 </em>

Thanks everyone for your kind words. For now I just want to reiterate in response to Illirikim:

I stand by my statement that Smolin’s story of the `prediction’ is fiction. I can tell you what my reaction was to the cc, because it was vivid: `Oh s**t, Weinberg got it right…’ There was no `Oh s**t, string theory got it wrong,’ because there was no such prediction. Had the cc been negative, there certainly would have been attempts to connect it with AdS/CFT – if the spatial curvature also turned out to be negative, AdS/CFT might have been a nonperturbative construction of our universe. But this would probably not be consistent with inflation, which requires a large positive cc early on.

On the stabilization (which Sean has well-described) I have agreed that there are open questions, and yes our current picture may not be entirely right. But it’s really an issue of how well we can calculate: if one keeps only the first approximation to the potential, it usually has some scaling property that makes it monotonic (no minima) so you have to work harder to get a controlled approximation.

Regarding the comment of Garbage: stabilizing moduli by adding non-perturbative effects in by hand does seem that way, but there do exist instances in which the moduli are stabilized completely by fluxes (and perhaps warping). Such instances lend themselves to a dynamical means of moduli stabilization. This area of string theory is trying to make experimental contact through cosmology, namely, the cosmic microwave background. In light of these ideas, it seems that to proclaim string theory a failure is a bit premature since to say so would suppose that it is a complete theory. I don’t think that anyone would affix their name to such a claim.

The content of a discussion that starts with “let’s stick to physics” should be “my theory predicts A, your theory predicts B, let’see who is right by doing this experiment”

Dear Prof. Polchinski,

Thank you for a very informative post.

Proponents of LQG, such as Smolin, often make the claim that a fundamental theory ought to also give a satisfactory interpretation of QM; they seem to suspect that the two problems, quantizing gravity and interpreting QM, somehow are related physically. I was curious whether you saw it as a valid critique of string theory that no framework for understanding QM at some deeper level (whatever that would mean) has emerged from it. Do you think that it points to something missing from the theory, or is it just not an issue?

a: that may be how science

shouldproceed in an ideal world. The mainstream hype of string theory is not based on a comparison of string theory results to those of loop quantum gravity or other alternatives.This is not a new problem. The mainstream theory is always defended first and foremost by elbowing contenders out of the way by pretending that they don’t really exist, aren’t serious, or should be seriously considered only after they have had as much time invested in them as the mainstream theory (which is a catch-22 situation, due to the lack of funding and lack of promotion of the alternatives).

Most people ignore alternatives because they don’t have the glamour of the mainstream.

In response to Nigel: Yes, there does seem to be a nasty tendency amongst some researchers to label other theories as vacuous or worse simply because they are not the pet theories of the most famous people in a particular field. Of course, most people don’t operate this way– but there is always a small and vocal minority of people in any area who will speak out against unconventional ideas. The truth is, at least in mathematics, it is not really a matter of who is “right” or “wrong”; it is what turns out to be elegant and interesting. Sadly, it does often seem that elegant and interesting ideas get dismissed out of hand as “crackpot ideas” before they have a chance to be properly developed- this seems unfortunate, but only to be expected– because, after all, there is also a great deal of chaff along with these few gems, and who really wants to sort through every half-baked scheme?

At the end of the day, most things with interesting structure and connections to other areas will find some application, somewhere– it just might not be the application for which the construction was originally intended. Research is like that– you might start by trying to use something to prove or establish something else and end up in a completely unexpected place. String theory might turn out to be a good example of such. Or, it could be an idea before its time; perhaps string theory contains seeds of a deeper truth within it but some “missing link” needs to be inserted between it and “classical physics”. I guess only time will tell what happens to all of these things.

I would like to rephrase the point raised by invcit #17. Since no approach to QG can make any reliable calculation about anything testable, one should at least demand that QG resolves the conceptual problems, e.g. the problem of time. Here is my favorite version:

* In GR, time is what a clock measures.

* In QM, time is a c-number parameter rather than an observable; according to Pauli’s theorem, a self-adjoint time operator is incompatible with a Hamiltonian bounded from below.

There is clearly a tension between these statements, since reading a physical clock is a physical experiment which must be described by an observable. It seems to me that the successful theory of QG must resolve this paradox, and that neither ST nor LQG is doing a particularly job at this. What hope is there to unify QM and GR, if you can not even unify the notions of time in the two theories?

Prof P said: “I stand by my statement that Smolin’s story of the `prediction’ is fiction.”

I think I can agree with that, while conceding that S is right about one thing: the positive CC came as a complete surprise, and it was a great pity that our theory of everything failed to give even a single clue that something so basic and momentous was afoot. It wasn’t a failed prediction, but it certainly didn’t look good.

I can tell you what my reaction was to the cc, because it was vivid: `Oh s**t, Weinberg got it right…’ There was no `Oh s**t, string theory got it wrong,’

Yes, I agree. With the last sentence, not with Weinberg getting anything right…..

Not quite Bohr vs. Einstein.

But then again, they are baby boomers, and like to pretend.

mollishka on May 21st, 2007 at 8:45 pm

asks:

“I’d like to step back and ask: what non-string alternative ideas are there that are being seriously considered to explain what the Standard Model doesn’t explain (which, I assume, is primarily having gravity finally get along with everybody else)?”

I have two comments in response to your question:

-First: At any energy that we have direct experimental or observational information about [up to the energy scale of inflation], gravity gets along with everybody else just fine. In fact, at laboratory energies quantum gravity is the most precisely calculable piece of the standard model. This is because it can be treated by Wilson’s methods of effective field theory; for a general review of the ideas of effective field theory see the first half of the review:

– Effective field theory and the Fermi surface. Joseph Polchinski (Santa Barbara, KITP & Texas U.) . NSF-ITP-92-132, UTTG-20-92, Jun 1992. 40pp. Lectures presented at TASI 92, Boulder, CO, Jun 3-28, 1992. Published in Boulder TASI 92:0235-276 (QCD161:T45:1992) e-Print: hep-th/9210046

For the explicit discussion of the effective field theory treatment of quantum gravity see the reviews:

– Introduction to the effective field theory description of gravity. John F. Donoghue (Massachusetts U., Amherst) . UMHEP-424, Jun 1995. 26pp. Talk given at Advanced School on Effective Theories, Almunecar, Spain, 25 Jun – 1 Jul 1995. e-Print: gr-qc/9512024

– Quantum gravity in everyday life: General relativity as an effective field theory. C.P. Burgess (McGill U.) . Nov 2003. 57pp. Published in Living Rev.Rel.7:5,2004. e-Print: gr-qc/0311082

What string theory does is to provide a consistent quantum description of gravity at arbitrarily large energies [the Planck scale and beyond], where the effective field theory methods would no longer be applicable. It should be noted that there are also aspects of the particle physics of the standard model which break down at very large energy [Landau poles in scalar self- interactions, fermion mass Yukawas, and the U(1) gauge couplings], so both Einstein gravity and the standard model of particle physics eventually have to be replaced with a more encompassing quantum theory at very large energies [beyond the range of (at least present) experiment]. Any proposed alternative to string theory would have to provide an extension that encompassed all of this physics.

Second: Within the standard model of particle physics there is a lot that is not understood. We have no understanding of why the quarks and leptons get the precise masses that they do; we have no prediction for the mass of the Higgs particle; we have no prediction of the values of the gauge coupling constants; we have no idea why the vacuum energy is so ridiculously small [cosmological constant problem]; we have no idea why the electroweak scale is so much smaller than the Planck scale [hierarchy problem]; we have no idea why there is no observable CP violation in the strong interactions; we have no idea why neutrinos have the masses they do; we have no idea why the mixing matrices in weak decays are what they are, both in the lepton sector and in the quark sector; we have no idea what composes the cosmological dark matter; we have no idea how the asymmetry between matter and antimatter, which we see in the universe today, was generated after inflation;…. There is a lot that we don’t understand; some of these questions may be answered in a “bottom up” manner (hence all the activity in the kinds of models listed in my post above), but others may require a unified theory like string theory to give a satisfactory answer.

After snaring the first comment spot with a silly not-quite-a-joke, I realized that Prof. Polchinski’s essay makes an observation which is relevant outside the field of quantum gravity research and, indeed, outside what we typically consider “theoretical physics” proper. I refer to the following:

Isn’t this exactly the process which popularizations (

vulgarisationsif you want to be Gallic) typically fail to address?A lot of talk. So so much talk. 500+ comments on the ‘string theory losing public debate” thread. But nothing new from 3 years ago on the string side, and the money keeps coming. The phenomenology people look at this and moves on. The math people can be forgiven to think string theorists have taken over their work. The cosmologists may want to increase the factual foundation of their field by not mentioning ST too much. The astrophysicists take a look and say “better to build real machines and observe”. The loop people don’t care and never did care. And the interested public, reflecting the recent talk by David Gross in Israel, take a look at that cartoon depicting the hamburger joint with the poster “Tonight. Is string theory bullshit?”, smiles and moves on.

dark-matter on May 22nd, 2007 at 10:58 am

writes:

“The loop people don’t care and never did care.”

Actually, this thread exists because one of the loop people appears to have somewhat of an obsession with string theory, and to be upset that most string theorists are sufficiently excited by progress in their own approach so as to feel no need to work on others. I would qualify the degree of interest that would motivate someone to take a large chunk of a year out of their own research program, just to write a non-technical polemic attacking the research program of others, as being, at best, not conducive to their own research.

There’s lots of research done that doesn’t particularly excite me. To take a random example, in my opinion large extra dimension models are problematic, for a variety of reasons. But I don’t write a book attacking them, and the people that work on them, rather I just work on theories that seem to me more likely to be right. I found some of the recent [last 10 years] conferences, which were largely dominated by LED talks, to be a waste of time, but that bandwagon just distracted people from working on the physics that I think is good, and which I then got to harvest without hordes of other people trying to do the same thing. Generally speaking if someone wants to write a book or paper on their own research, that I find interesting and often worth my time to read. If someone is writing a book just to attack the work or character of others, that I find to be a complete waste of time, and my advice would be to instead put that time and effort into improving their own research program.

P.S. you also write “and the money keeps coming”. Actually, numerically, string theory is a relatively small perturbation on particle physics. Any reasonable attempt to count active string theorists would probably get less than 2000 world-wide. This is certainly less than the number of active particle phenomenologists, probably less than the number of active astroparticle theorists, probably a factor of 3-5 less than the number of active theoretical astrophysicists [I don’t have any feeling for the number of active observational astrophysicists / astonomers], and it doesn’t even add up to the number of scientists on ONE of the LHC experiments [I think that CMS now has over 2,500 people on their author list; the 4 LHC experiments between them count something like 7000 scientists]. This is as it should be: the experiments that will carry our understanding forward need, and deserve, the largest slice of support, and in a healthy scientific ecosystem theory that connects directly to experiment has to be encouraged. Rather than making snide comments about support for other types of research that you personally don’t like, perhaps a more constructive approach would be to make the case for increased research support for the full range of fundamental physics, including the type of research that you undertake.

#17 just a historical side remark reg Kaluza-Klein: as far as I recall Klein did not have the radion because he simply set the g_55 entry to be equal one. Kaluza had, but he was working only in a linear approximation and he did not talk about compactification – instead he had what he called the ‘cylinder condition’ which kind of artificially set derivatives wrt to extra coordinates to zero (that is, he dropped all excitations).

“And the interested public, reflecting the recent talk by David Gross in Israel, take a look at that cartoon depicting the hamburger joint with the poster “Tonight. Is string theory bullshit?”, smiles and moves on.”Nah. At least not the interested public I know. Some writers and bloggers may say that, but the reality I see is that the interested segment of the public is not particularly vested in any given outcome but is increasingly interested in the debate itself. See, none of our funding depends on the outcome….;o)

In fact among the laypeople I know who think about such things I don’t know a single person who holds anything like a “belief” regarding string theory: that it is true, or is false, or anything. We are interested, probably more so now than ever, but unconvinced either way. It’s a very interesting “maybe;” the change in the debate is that now there are competing perspectives that are better know to us.

This situation can’t go on forever of course. At some point people will tire of a endless debate without at least some experimental resolution, and that point will come much sooner if the debate takes on a flamey edge with explicit discussions of who deserves tenure and funding and who does not based on which camp they are in – something I know is important, and real, and relevant. But the one thing I can guarantee you with absolute certainty is that

the taxpaying public does not want to see inside your sausage factory. This is not a winnable debate for either “side” if it is held in public – the debate itself is a losing effort.I say this out of deep respect for all of you and the work you do.

If you all can keep the debate on topic (the science itself), and at a ~50% comprehensibility level for those of us without the math (which you’re all doing great at BTW, it’s fine for individual posts to go much lower that that), I am completely certain that this debate will energize rather than sap the public’s interest in the frontiers of physics.

Of course, the “winner” can only be determined by predictions agreeing, or not, with experimental outcome. The semantic debate is fascinating but ultimately of limited relevance in the long run…though it gives us something to do until the LHC comes online.

(great /. link today on the many petabytes of expected LHC data and the issues that raises, BTW, very interesting stuff)

Lee Smolin:What we are dealing with is a sociological phenomenon in the world of academic science. I do think that the ethics of science have been to some degree corrupted by the kind of groupthink explored in chapter 16, but not solely by the string-theory community. For one thing, it is the academic community writ large that makes the rules. In a court of law, a good lawyer will do anything within the law to advance the cause of his clients. We should expect that the leaders of a scientific field will likewise do everything within the unwritten rules of academia to advance their research program.A couple of things caught my attention in Joe’s response to Lee.

One in regards to the view of mathematics as the basis, beyond what ideas are first presented.

I couldn’t help but think that any ideas expressed in science here, having a mathematical basis, would set the course for “new ideas to come forth” and create a new basis of thinking, now having this new view of the world. It would have ignited new mathematical directions with which to develope those new ideas.

If one had said certain limitation in regards to Mandelstam’s Finiteness, then the limits of that discussion would have been a point made by Joe in regards to the distance with which this mathematics had been taken. Lee ideas would have been shown to limit what he had to say in face of what Jacques imparted to him.

Jacques Distler:This is false. The proof of finiteness, to all orders, is in quite solid shape. Explicit formulΓΒ¦ are currently known only up to 3-loop order, and the methods used to write down those formulΓΒ¦ clearly don’t generalize beyond 3 loops.This has brought us to the difference in opinion of the mathematical basis and hence the proof that Lee’s coments in this regard are limited in regards to the expression of his ideas?

sorry, #17 in #27 should have read #11.

Interesting press release from the Perimeter Institute today; Howard Burton, their director who hired Smolin as their first staff scientist, is out. Here it is:

WATERLOO, ON, May 22, 2007 – It was announced today that Howard Burton, Executive Director of Canada’s Perimeter Institute for Theoretical Physics (PI), will be departing the organization in the near future. The search for an interim leader and long term successor will be conducted through collaboration by the Board of Directors, the Institute’s Faculty, and the preeminent Scientific Advisory Committee….

{full announcement at:

http://www.perimeterinstitute.ca/News/In_The_Media/News_Releases/

just look for the first item on the page: “PI’s Executive Director to Seek New Challenges “)

Joe Polchinski’s review of Peter’s and Lee’s books was a highlight of the debate. The positive spirit and cheerful love of physics was everywhere present in what Joe wrote then.

The new reply by Joe is very interesting, and raises a lot of points for discussion, but it does not raise to the the level of his original review. Joe “took off the gloves” this time, made all sort of rhetoric punches, and it was both prettier and more convincing, when he had the gloves on.

Here are some points based on some of Joe’s “great lines for discussion” :

1. Joe wrote:

A chain of reasoning is only as strong as its weakest stepThis statement whether applied to evaluate a whole scientific theory or a specific argument is an extremely interesting issue in philosophy of science. It arouse in various scientific controversies from archeology to biology.

While it is formally true that the strength of a scientific argument or a scientific theory is as strong as the strength of its weakest link (or step), in my opinion this is not really true. It is perhaps fair to say that the strength of an argument (or a theory) is not weaker than its weakest link but there are cases it can be stronger. There are cases the strong links give extra support to the weaker links.

Certainly Joe’s line is not so positive when it comes to string theory. Some of the links (or steps) are not only weak but yet non-existing.

2. Maldacena again.

I share the opinion that there is no way one can attack string theory as a whole based on Maldacena’s conjectures which are a great triumph for string theory. (And I criticized Lee’s approach on this point.) But I do not see anything wrong with a research program aimed to find weak points in or counter arguments to the strong Maldacena’s conjectures. Lee raised the possibility that the validity of the weak form of Maldacena conjecture accounts for strong symmetry that is not present in the general case. In his book Lee raises this possibility (along with some other legitimate concerns) as an idea and not as a proved fact. This is fine. Joe is critical about several of Lee’s ideas concerning the strong Maldacena’s conjecture and that is fine as well. Joe even note that some of Lee’s coauthors have papers where they present evidence which goes against Lee’s approach, this is very fine.

If indeed Joe’s shot down three specific suggestions that Lee had made, this is quite interesting but Joe’s critique of Smoling’s research efforts regarding this matter as

a priorimisguided is not clear.3. Joe wrote about rigor:

In physics, which is a process of discovery, this can make them [rigorous result] worse than useless,Joe’s anti-rigor argument comes across as a little strange. It is certainly correct that string theory is not required to have stronger levels of rigor than that of highly successful physics theories and methods on which it is based. There is always the hope that the advances on the physics side (and sting theory itself) will help putting these methods and theories on more rigorous foundations and there is always the concern that the non-rigorous nature of the methods will cause them to collapse for such a far far reaching extension of their original usage as string theory is.

If there are scientific reasons to reject the argument based on “Rerehn duality” that is fine, but what does it have to do with rigor in general? It is justified to claim that there are good reasons for non-rigorous nature of string theory as it is fine to point out that there are good reasons for the difficulty to make predictions in sting theory. But, in my opinion, it does not come across very well when (even justified) weaknesses are portrayed as advantages.

4. Joe wrote:

This process of translation of an idea from words to calculation will be familiar to any theoretical physicist. It is often the hardest part of a problem, and the point where the greatest creativity enters. Many word-ideas die quickly at this point, or are transmuted or sharpened.

This is a great description! wow!!!

(It also relates nicely to Lee’s point regarding the different approaches in physics of 1960-80 and earlier physics.)

5. Three points that I’d love to hear more about:

Joe’s explanations on duality, on the UV finiteness of string perturbation theory and, his point regarding the larger and smaller spaces concerning the constraints, are extremely interesting (but rather condense and cryptic) and it will be great hearing further explanations on these issues.

6. Anecdotes and quotes:

Lee anecdotes and quotes (one even from a Cosmic Variance’s blogger,) regarding string theory and string theorists gave very very little support to his overall argument. And by the same token also Joe’s anecdote concerning his discussions with Lee that are not documented in Lee’s book are not really damaging to Lee’s argument. All these matters are very very very side issues.

7. In summary, overall, the scientific debate/discussion regarding string theory and related wider matters is quite good (and it is becoming overall better) and interesting. Peter and Lee deserve a credit for igniting this discussion. I also join the others thanking Joe.

One strange aspect of this discussion is that we hardly see any retractions. In “normal” scientific discussions (like between scientific collaborators) a statements like “I was wrong on this point”, “this was a silly idea, let me try something else” can account for 80 percents of the discussion. Here, we do not see anything of that kind, even regarding small side-issues.

Gina on May 23rd, 2007 at 3:40 pm

writes:

“Three points that I’d love to hear more about: Joe’s explanations on duality, on the UV finiteness of string perturbation theory, and…”

The first two are textbook material. Dualities are well treated in Johnson’s book on D-Branes. The fact that the prospective uv divergences in string theory are really ir effects is scattered in various texts [I assume that it’s in Polchinski’s but I don’t have my copies at hand to check].

Beyond that I disagree that “the scientific debate/discussion regarding string theory and related wider matters is quite good”. Basically I disagree that this discussion, as presently conducted, is really even scientific; as Polchinski noted:

“In my review I have gone through your book and papers and identified three proposals, and explained why each is wrong. Again, you have not acknowledged the existence of scientific counterarguments, but have just reasserted your original point. If your arguments had been made in a serious way, I would expect that you would have given some deep thought to them and be ready to defend them.”

That’s not science. And it’s sad that a scientist as distinguished as Joe Polchinski has to take time away from his own research to defend his field against distortion and misrepresentation in the popular press.

Thanks again for the comments and support.

invcit #17

This is an interesting question, to which there is no definite answer. On the one hand, since it was possible to quantize the other three interactions without changing the interpretation of QM, it is not obvious that one should not be able to do the same for gravity. If we restrict to `laboratory’ experiments with gravity (even building black holes in the lab), there is no sharp paradox that would require us to modify QM. QM makes us queasy, but if it gives consistent predictions for all processes we may just have to live with that. Things are much less clear when you get to cosmology. Chaotic inflation, for example, does seem to lead to paradoxes, which might be the clue to a deeper understanding of QM.

Tyler #28 and Gina #32,

I am glad that you are enjoying the physics, and I agree that this is the fun part. But Smolin’s book was presented as a discussion of the sociology of science with string theory as a test case, and many people have taken his arguments seriously. Thus I must also respond to this. In particular, this point about the existence of the gauge theory: The Wilsonian understanding of quantum field theory is one of the centerpieces of theoretical physics, and has been the area of some of my best work: the reformulation of renormalization theory, and the effective field theory analysis of Fermi liquid theory and BCS superconductivity (both outside of string theory, by the way). Regardless of who said what to whom, for Smolin to simply dismiss this subject as sociology and groupthink is outrageous.

Gina – I don’t want to beat this subject of rigor into the ground, but your commentary about my statement `A chain of reasoning is only as strong as its weakest step’ is on the mark. A good physical argument can indeed strengthen the links around it; a rigorous argument is generally very rigid in scope and cannot do this. Also, rigorous arguments are generally constructed as chains, so the weaknesses add in series. Physical arguments are in general webs, with a complex interweaving of arguments – certainly the argument for Maldacena duality is of this type: for it not to be true, one would have to tear many strands.

Prof. Polchinski, I have to take issue with your statements regarding mathematical rigor:

Yes, the concepts must be defined clearly, the logic unbroken. I would have thought that since that made the results reliable, it is something to be desired, not spurned.

Loose thinking with ill-defined concepts is fine during discovery, but once your physical mechanism is discovered (and you can only claim discovery after experiment confirmed your predictions), you need to analyze it to properly understand it. That means that you have to get your logic straight, i.e. make it rigorous. How else can you clear the fog?

Loose thinking and bad applications are not the fault of rigorous results;- “it is a bad carpenter who blames his tools.”

A rigorous reconstruction of a piece of physics clarifies and polishes the physics. Moreover, it can often reveal aspects of the problem which were hidden. I cannot see how you can fully understand a piece of physics without having made it rigorous. So it is not possible to “understand the physics very well” without this. Of course it can be done badly, e.g. by choosing irrelevant features of the physics to build on.

..in the same way that a fog is robust;- it can accommodate anything. In fact, ultimately a rigorous mathematical result is far more enduring. It is harder to establish, but you can build on it wherever its initial assumptions apply.

How can an ill-defined version of an argument be better than a logically clear one?

So once it is established, it can be relied on, and truth carried along the chain from the start to the end.

Where most of the arguments are ill-defined and made up of analogies, and cannot give a true understanding of their subject.

It is a pity that in your remarks you see this conflict between logical rigour and physics theorising. As I indicated above, I do see a place for the nonrigorous approach of physics in the process of discovery. However proper understanding can only come from clarifying the concepts and their relations in a rigorous way, in fact, this can lead to subsequent discoveries.

Since string theory presently seems to be speculative physics (the well-known lack of experimental confirmation), one would have expected that you should try to make its internal logical structure as solid as possible. Unfortunately, it seems the handful of papers produced by mathematical physicists on string theory topics are mostly ignored (e.g. Dimock, Wiesbrock etc.), and in the case of Rehren seems to be controversial. I think rigorous approaches can also offer alternative approaches to circumvent some problems of string theory, but these are lost on the community.

What a gem!

Beautiful!

I am most grateful to Prof. Polchinski for sharing his thoughts. When commonly held wrong perceptions are not debunked in such a clear, dispassionate manner, it is taken to be true by many outsiders (like myself).

It is clear that string theory is a remarkably deep field (the deepest there is, in my opinion), and many should continue pursuing it.

It seems to be much less convincing (if at all) in its original purpose of understanding/explaining particle physics. Of course, it is true it is superior to the effective field theories of particle physics since it UV completes it.

What I mean is that it does not offer any specific guidance on particle physics models (sure there are brane-world models, KK models etc, but a lot of it following from QFT itself). For example, as far as I know, it does not restrict the possible 4D QFTs (beyond what is prohibited by QFT itself). Actually, I suppose, string theory does assert that the 4D effective field theories cannot be compactified from a, say, 320-dim QFT. So only certain KK towers are allowed. Is that correct? Still would leave a lot of possibilities, but is at least a restriction…

Considering the large hierarchy, it seems unlikely (to me) that it ever will (e.g., chemistry from the standard model).

PS:

Wicked

Pingback: String Theory: Not Dead Yet | Cosmic Variance

Dear Prof. Polchinski,

Thank you for your comments.

Could you please expand a little on what you meant by that chaotic inflation seems to lead to paradoxes that could be relevant for the interpretation of QM or point to a paper that discusses this? It sounds very interesting.

Thank you!

Dear All,

This has come at the worst possible time for me to reflect and reply, so I will not be able to reply quickly and in detail. I thank Joe for the response, there are many points where I would like in time to comment, and others on which we simply have differing scientific judgement. There is nothing wrong with having differing scientific judgements, nor with debating why we take different points of view about open questions. So I thank Joe for taking the time to reply.

It is distressing to however read comments such as the following, “for Smolin to simply dismiss this subject as sociology and groupthink is outrageous.” Anyone who read the book would know that that is not at all what I did. The first 3/4 of the book are straight science and history of science, and the analysis of the strengths and weaknesses of string theory is done there completely on scientific grounds. And there are lots of places where I acknowledge the interest and importance of substantial results about string theory. The assessment of string theory and various claims about it given there is mixed, and balanced. Many successes are mentioned, as are several problems. It is a complex picture, with strong pros and cons, and the open questions are genuinely puzzling. That is why it was worth writing a book, to sort out what to make of it. I am extremely tired of comments which ignore the complexity of the subject and imply also that I ignored it. The useful discussion only starts when someone acknowledges that there are strong reasons for interest in string theory AND also strong reasons to be skeptical that it is the theory of nature.

The discussion of sociology is only in the last of four parts of the book. And there was nothing there that was at all new to people who study the sociology of academics, or experts in general. I am surprised that anyone finds what I wrote surprising.

Joe mentions some standards: “To what extent are known difficulties acknowledged? When a new counterargument is given, is it addressed, and the original assertion modified if necessary? Are facts presented in a clear and direct manner?” I agree these are important standards and I believe I have satisfied them. That is the reason why the assessment of string theory in the book is mixed and balenced. The whole book is the result of such a process, carried out over twenty years of work on and study of the subject, with many discussions with string theorist. Indeed, the book does not contain every argument I made or even published about string theory, precisely because my arguments have been altered by progress in the field as well as improvements in my understanding.

For example Joe mentions here and before my paper with Matthias Arnsdorf on Rehren’s version of AdS/CFT, hep-th/0106073. I would be happy to discuss this, but please first notice that I do not mention the argument of the paper in the book. This is because we realized since posting the paper that there is an important difference between Rehren’s version and Maldecena’s version of AdS/CFT that makes a comparison between them less useful. This has to do with whether the special conformal transformations have anomalies or not. Rehren’s construction is rigorous but because special conformal transformations remain non-anomolous it does not apply to the context of Maldacena’s conjecture.

One way to acknowledge difficiculties in arguments is not to trouble people with them again. So I wish you had noticed that the argument of that paper was not part of the book, and not made an issue of it.

Further, in a few cases, such as the study of heavy ion collisions with AdS/CFT I have acknowledged that important things have happened since the book was finished.

At the same time, it is also necessary that I discuss the extent to which these new results change the overall assessment of the promise of string theory to resolve the 5 major problems I gave in the book. And, for reasons I explained earlier they do not very much. This is because having a phenomenological model of QCD at high temperatures is not one of the five big problems that my book is about. I only discuss string theory there as a candidate for an answer to those questions, and if it happens that some aspects of string theory can help with another question that’s great-we are in the midst here of a very interesting workshop about that. But it does not obviously change the assessment of string theory in relation to the 5 big questions.

My book was concerned only with our progress towards answering those 5 big questions. Most of phsyics is outside of that. If part of string theory is relevent to heavy ion collisions, wonderful, well worth working on. But I have heard no logical argument that this increases the likelihood that it is the fundamental theory of nature. Newtonian physics has many applications but it is not the theory of nature.

Out of everything else, let me just quickly respond to one assertion:

“I have recently attended a number of talks by leading workers in LQG, at a KITP workshop and the April APS meeting. I am quite certain that the standard of rigor was not higher than in string theory or other areas of physics. In fact, there were quite a number of uncontrolled approximations. This is not necessarily bad – I will also use such approximations when this is all that is available – but it is not rigor.”

This does not acknowledge that in any subject the level of rigor is mixed. If you hear a talk by me you get a presentation of work with much less rigor than in a talk by Thomas Thiemann. In string theory as in other subjects there is a range of rigour.

I made no claim that the subject of LQG has a uniformly higher level of rigor that string theory. I did claim that there are a collection of rigorous results proved by mathemtical physicists, and that they include existence and uniqueness theorems which anchor the foundations of the subject. This is important, first because it does put the subject of LQG on rigorous foundations, second because it refutes the impression that it is useless to require the presence rigorous results in justifying an approach to quantum gtravity.

Thanks,

Lee

Dear Lee,

Will you address the first point of Joe’s response about the “fictitious prediction of a non-positive cosmological constant”?

Thank you!

Dear non-of-the-above,

Thank you for your comments on physics. You did not agree that the discussion is scientific. I see matter differently and let me try to explain my point of view. (Perhaps I should have referred to the discussion as “academic” rather than “scientific”.) Anyway, while the discussion has some components which are neither scientific nor academic it does have some scientific components which are, in my view, of value.

You referred specifically to what Joe’s wrote

“In my review I have gone through your book and papers and identified three proposals, and explained why each is wrong. Again, you have not acknowledged the existence of scientific counterarguments, but have just reasserted your original point. If your arguments had been made in a serious way, I would expect that you would have given some deep thought to them and be ready to defend them,”

and concluded “That’s not science”. I beg to disagree especially on the example you have raised.

Joe indeed described in his original book review (not in the main body of the text but in footnote [3]) his critique on two papers by Lee Smolin (one with Arnsdorf). Joe’s critique is quite concise and is given in plain English (with heavy physics accent but without any calculations.)

That’s no science, you said; on the contrary, dear non-of-the-above: A critique offered by a well-known physicist on two papers written by other well-known physicists is a very nice and welcomed scientific contribution. (Even if not representing a cutting edge science.) These weblog discussions are quite a good place for such a critique to be made. (It is quite unlikely that Joe would have bothered to write a paper about his critique). It is especially important if Joe’s short remarks indeed definitely show that these (rather long and extensive) papers or some of their central ideas are flawed.

Two additional points

1) As it turned out, Lee also regards by now the argument in the paper with Arnsdorf as less convincing, and was not referring to it in his book. (Probably it could have been useful for Lee to acknowledge the weaknesses that he realized after publication in a new archive version of the paper or something of that kind and not just wait to a weblog discussion.) I do not know if Lee agrees to Joe’s specific points also regarding another large overview paper of him on quantum gravity.

2) It is sort of interesting that Lee’s paper attracting such a scientific response (and in this case a critique which Lee may even agree with,) was a consequence not of the papers themselves but rather of Lee’s book and “anti-string” campaign.

Dear o,

I will address it, but please keep in mind that I am in blog mode, I don’t have time as I usually do to check sources. Here is what seems to be not in dispute:

-There was a problem in the period 1998-2003, there was an observed positive vacuum energy and none of the known solutions or vacua of string theory had that property.

-Some people perservered trying to solve it.

-It was solved in 2003 with the KKLT and following papers (in the context of a certain semiclassical approximation.)

-A consequence was that there were 10^500 distinct vacua that solved the problem, to the same approximation.

I don’t see how it can be in dispute that there was a problem in the first place, otherwise the KKLT paper would not have had the significance it did.

What is the dispute about? Joe and I have different reminiscences as to how optimistic or pessimistic the people we read and talked with were about it. That is natural, it is usually the case with key unsolved problems. I can call on lots of evidence that some people saw this as a serious problem, even a crisis, Joe can call on lots of evidence that others were nontheless optimistic. There is no contradiction there, this kind of diverse opinion is, as I argue in the book, not only endemic in science but healthy and necessary for the progress of science.

It is in fact a bit annoying that Joe claims I have my facts wrong when what is at issue is that different people had different judgements at the time.

Joe if I recall correctly, in his first review argued that the problem was not believed to be serious in his community. He then argued it could not have been taken seriously because any solution would involve two further unsolved problems: supersymmetry breaking and moduli stabilization and people were working on them. Indeed, there were recent ideas about them using branes and dualities and these were being explored. In fact, this is how KKLT and others eventually solved the problem.

Since the problem was solved, Joe’s optimism turned out to be more reliable than my pessimism in that period. That is not in dispute, any one who thinks it is misunderstands the role this episode plays in my book.

I am interested in the story because it involves a repetition of a logic that we first encounter in Part I when I tell the story of the first higher dimensional unifications. The logic is that higher dimensional unifications lead to two big issues: instability of compactifications and freedom to choose many compactification topology and parameters. Recall that I emphasize that Einstein basically understood these were problems in the 1920s and the result at that time was his loss of interest in Kalaza-Klein theories.

My point is that the same problem reappears in string theory, but in spades. The meaning of KKLT is that the cost of solving one of these problems (stablization) is to make the other problem (freedom and lack of predictibility) much worse.

So the crisis in predictability that led Susskind et al to revive my proposal of the landscape has its routes in the basic issues of higher dimensional unifications- instability and increase in parameters-identified first by Einstein in the 1920s and confirmed in dramatic form by KKLT in 2003.

The question is then what is the cost of this trade off. The conclusion I draw from this is that the cost of higher dimensional unifications is too high, because it results in a lack of predictability.

Indeed, I should emphasize that the problem is never completely solved. The reason is that the kind of SUSY breaking involved raises the vacuum energy rather than lowers it, as in many other examples of symmetry breaking. Thus, solutions with positive vacuum energy with broken SUSY are generically unstable.

So KKLT solutions with positive vacuum energy are all unstable, the issue is only for how long they remain excited. Applied to nature, this is either a bold or a foolish conjecture, time will tell. But it is not surprising that many worried that it could be pulled off.

I hope this goes some way to addressing the issue.

Thanks,

Lee

RE: Polchinski [and Bousso]

a – considering systems of planets within solar systems and these within galaxies, their concept of nested bubbles is very possibly correct.

b – their concept of lowest energy levels may have to be modified to equilibrium energy levels.

RE: Smolin

c – LQG may be similar to loop planetary gravity which has only an axial perspective. If there are three spatial dimensions then there should also be sagittal and coronal perspectives tending to be sinusoidal because of helicity.

d – spinfoam may have to be modified to twistfoam, adapting Penrose terminology,

Gina on May 24th, 2007 at 3:56 pm

wrote:

“You referred specifically to what Joe’s wrote

“In my review I have gone through your book and papers and identified three proposals, and explained why each is wrong. Again, you have not acknowledged the existence of scientific counterarguments, but have just reasserted your original point. If your arguments had been made in a serious way, I would expect that you would have given some deep thought to them and be ready to defend them,”

and concluded “That’s not science”. I beg to disagree especially on the example you have raised.”

Dear Gina

I believe that you have misinterpreted my point; perhaps I did not express myself clearly, and I’m sorry if my post was confusingr. My comment “That’s not science” was not directed at Polchinski’s post; even a popular explanation from Polchinski is science of a high standard. What I was referring to as not being science was that Smolin had not “acknowledged the existence of scientific counterarguments, but have just reasserted your original point.” When someone has refuted your arguments you don’t just ignore the refutation because you don’t like the conclusion. That’s not science.

P.S. You also make the following comment:

“2) It is sort of interesting that Lee’s paper attracting such a scientific response (and in this case a critique which Lee may even agree with,) was a consequence not of the papers themselves but rather of Lee’s book and “anti-string” campaign.”

You need to put this in context. Every morning every working physicist in this field logs onto the “Los Alamos” archives [http://www.arxiv.org/], to get access to all the new papers appearing in the last 24 hours. On an average morning I read the titles and abstracts to the new papers in: hep-ph (particle phenomenology; average 20 papers), hep-th (formal particle theory; average 20 papers), gr-qc (gravitation and cosmology; average 10 papers), and astro-ph (astrophysics; average 40 papers). So on an average morning I read the titles and abstracts to somewhere between 50-100 papers. Of that group there are typically 2-4 papers which I download to read in their entirety (some I skim, others I will work through line by line over several days). Also, of that group there are typically at least 5-10 of them, on any given day, that after reading the abstract I think to myself “that doesn’t sound right”. I don’t download those papers to actually work through them to find out why they’re wrong; it’s a waste of time to read wrong papers, and with the volume of literature one needs to deal with every day time is very valuable. Wrong, or irrelevant, papers, don’t get extensively discussed and refuted, people just ignore them and read the good papers, of which there are already enough to eat up huge chunks of your time. So it’s not surprising that the paper of Arnsdorf and Smolin was so thoroughly ignored; that’s the way active workers in the field pass judgement. But when the approach to AdS-CFT duality proposed in that paper becomes the centrepiece of a popular book attacking string theory and seeking to undermine support for the field, then for the health of the field leading experts in the subject have to explicitly address why this work is wrong. This is a waste of Polchinski’s time; he is one of the world’s leading theorists, and one of the people whose papers I will automatically download and read if I see one on the archive in the morning. I would rather have Polchinski writing papers on his own original work, than wasting his time debunking dubious papers from lesser physicists. But by taking their attacks public in popular books Woit and Smolin have made such a non-response dangerous to public support for the field. That is why someone of Polchinski’s stature had to reply, and why in my first post above [Number 4] I wrote to thank Polchinski for his time and effort in doing this.

dear none-of-the-above,

First, I did think about and respond carefully to Joe’s arguments. It is just not true that, I “have not acknowledged the existence of scientific counterarguments, but have just reasserted [my] original point.” Read what was actually written, please.

For example, regarding the full quote in context, “In my review I have gone through your book and papers and identified three proposals,…” this is refering to proposals for alternative forms of AdS/CFT duality. Here we have apparently been talking past each other. My point is that the strong form cannot be regarded as proven or even well formulated, because it posits an isomorphism between two mathematical objects that are not yet precisely defined, and which have not been shown to exist. These are facts, I don’t see how anyone could disagree with them. There is no precise non-perturbative definition so far of either side of the duality. Therefor there can be no proof of the conjecture.

Joe says that it is hard to find a weaker conjecture that accounts for all the evidence. Even if that were the case it doesn’t change the first point.

I do suspect that there is a weaker conjecture that is consistent with all evidence, let me come back to that sometime when I have time to think it over carefully. Its a scientific question, more a subject for a paper than a blog entry.

There is much else that Joe says that distorts the facts as I understand it, for example, “You raise the issue of the existence of the gauge theory…. First, Wilson’s construction of quantum field theory has been used successfully for 40 years. It is used in a controlled way by condensed matter physicists, lattice gauge theorists, constructive quantum field theorists, and many others. To argue that a technique that is so well understood does not apply to the case at hand, the scientific ethic requires that you do more than just say Not proven! Sociology! as you have done. You need to give an argument, ideally pointing to a calculation that one could do, or at least discuss, in which one would get the wrong answer.”

The issue is where is the burden of proof and what Joe says here is shocking. IN physics or math the burden of proof is always on someone proposing a strategy to show that it works in detail.

In fact serious attempts have been made to construct a lattice gauge theory with extended supersymmetry in 4d and all have so far failed. it is true that some progress has been made in lower dimensions, but in d=4 I have been told by experts that the issue is at best open and unresolved, after significant effort.

The alternative is to try to use a lattice theory without supersymmetry and tune the theory so that it approaches a fixed point with superconformal symmetry. This is a strategy, which might or might not work.

My assersion is only to point out that there is no non-perturbative construction or definition of N=4 SYM. Joe seems to say that the burden on proof is on me to show why there can be no such construction. I am sorry but the burden of proof is the opposite, it is one thing to argue for a plausible strategy to do something, but it is quite another to have followed that strategy to a definite result. Many well motivated strategies fail in mathematics and physics, so the burden of proof is on the person proposing it to actually carry it out. After all, if it were straightforward, than given all the thousands of papers written assuming the truth of this conjecture, someone would have done it.

Now, back to Rehren one more time: regarding, “But when the approach to AdS-CFT duality proposed in that paper (i.e. Rehren) becomes the centrepiece of a popular book attacking string theory and seeking to undermine support for the field, then for the health of the field leading experts in the subject have to explicitly address why this work is wrong..”

Where is this fantasy coming from that Rehren or my paper with Arndorf has anything to do with my book, let alone “becomes the centrepiece” of it. Did you both not read my book and not read what I wrote above?

That paper is not mentioned anywhere in the book, for the reasons discussed. It is true that I chose not to discuss Joe’s discussion of that paper in his footnote, but for lack of time and space I indicated everything could not be addressed. Since that paper was not a part of the argument in the book Joe was critiquing I chose to ignore that. Now I have dealt with it.

Lee, this is from pages 153-54 of your book:

“String theory could not explain why the cosmological constant was zero, but at least it explained why it was not a positive number. One of the few things we could conclude from the string theories then known was that the cosmological constant could only be zero or negative. I don’t know of any particular string theoriest who predicted that [it] could not be a positive number, but it was widely understood to be a consequence of string theory. The reasons are too technical to do justice to them here.

. . .

You can imagine the surprise, then, in 1998, when the observations . . . began to show that the . . . cosmological constant had to be a positive number. This was a genuine crisis, because there appeared to be a clear disagreement between observation and a prediction of string theory. Indeed, there were theorems indicating that universes with positive cosmological constant . . . could not be solutions of string theory.”

Those are strong statements, and that argument is plainly the most persuasive thing in the book.

You’re claiming the existence of both a) a consensus about a particular conclusion of string theory; b) a consensus that string theory was in trouble because of the positive cosmological constant. These are claims that should be verifiable, if not with certainty, then at least to the extent that you have a basis for them. Surely there must be SOME string theorist willing to say there was a consensus that the positive constant observation was at least a threat to the theory if not a crisis. I am not a defender of string theory, but I think the burden of proof is on you with this one, and it hasn’t been met yet.

Dear non-of-the-above,

“What I was referring to as not being science was that Smolin had not “acknowledged the existence of scientific counterarguments, but have just reasserted your original point.” When someone has refuted your arguments you don’t just ignore the refutation because you don’t like the conclusion. That’s not science.”

I understood what you meant. My comment was that Joe’s comment was a scientific remark exclusively made for these blog discussions, and these blog discussions are tailored for such remarks. I did not think it is significant that Lee did not respond to this particular point, and by now he did respond. My comment 2) was just an observation, not a critique of any kind, and putting aside these particular papers by Lee, I think your detailed description makes sense.

Has ‘dark-matter’ not read (for two examples) Brian Greene’s or Lisa Randall’s books?

They are examples of publishers making a darn good deal out of positive and inspiring presentations of string theory.

For you to then demand that Joe (or anyone else!) should write and publish a popular-level book to justify any statement they make about the state of the field is pathologically unreasonable and absurd. The fact that a publisher can make money out of a popularizing book has essentially no correlation with the correctness or usefulness of the statements made in it!

Curiously enough there isn’t a single book which succeeds in popularizing LQG or its relatives. But I think this is not necessarily a bad thing, and can even be justified by the fact that it is harder to get a first intuitive physical picture of LQG than it is of string theory.

This is the key to the problem: should mainstream hype be attacked or should rival theories be hyped like string theory? Professor Smolin has previously tried to popularise alternatives in books like

Three Roads to Quantum Gravity, but such books fail (like academic books on loop quantum gravity, such as Rovelli’s), to really combat string theory.In his lecture series (available at Perimeter Institute website),

Introduction to Quantum Gravity,Prof. Smolin does make the point very clearly that loop quantum gravity is an effective model for interactions between gauge bosons that carry energy and thus are a source of gravitation (i.e. gravitons carry a quantum gravity charge) as well as mediating gravitational interactions. Normally, the fact that gravitons should carry a gravitational charge makes their interactions crazy at high energy.The key fact is that you can get background independent (metric-less) general relativity from quantum field theory by summing interaction graphs in a Penrose spin network. That alone is impressive thing about LQG. What is interesting is that this result of LQG should apply to other things too; any field with gauge bosons which carry a charge. In the standard model, electromagnetism is mediated by uncharged photons, and this is supposed to be reason why electromagnetism is renormalizable. However, it might be the case that electromagnetism and gravity are related in a different way. For example, the U(1) part of the standard model might not be correct. It’s inelegant to explain with extra polarizations how an electric field can be either positive or negative if the gauge boson responsible is neutral. A simpler way would be to replace the standard model’s U(1) by a second SU(2), but this time with entirely massless gauge bosons: one positively charged (giving rise to positive electric fields), one negative (giving negative electric fields) and one which is neutral (giving rise to gravity). This scheme incorporates gravity into the standard model and makes predictions. Another option might be to modify the Higgs mechanism so that just a single SU(2) group produces both short range massive W+/- and W gauge bosons for weak interactions, and mass-less versions of those which mediate electromagnetism and gravity, respectively.

Thomas D:

You name ’em I read ’em. Not just popular books but papers. Going back 35 years I might add. I don’t demand anything from anybody. Prof Polchinsky is fully able to decide what he wants to do without you defending him using yet another group-think insult. Prof Polchinsky responses in CV are to Smolin book on ‘troubles’, not on LQG. Clearly he feels further debate on this already well-debated subject is useful. The logical next step in rising to the challenge is a book. After all, Prof Susskind wrote a book to promote the delusional illusion of string-inspired cosmic landscape and argued that the next frontier of science is anthropic worship, which Prof Smolin and others disagree. He responded with TTWP book. Interesting that we haven’t heard too much about this aspect of string nonsense since. So if Prof Polchinsky boss at KITP presented the question “Is string theory bullshit?” in a recent conference on ST, a credible response could be a book of the same class as above. Surely, after so many years of string work, so much energy and money invested, a semi-popular book presenting the great discoveries of ST, summarizing the results and presenting a bright future can be written? With thousands of researchers in the field, consuming hundreds of millions of dollars of public money, cannot one authoritative figure stand up to face accountability? (I don’t regard Greene and Randall books as string books.)

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Dear Amos,

Exactly who thought what and how many worried or were confident is an interesting question for an historian of science. However, I have a strong memory of worrying about this after conversations with string theorists and after reading Witten’s paper hep-th/0106109,written in 2001, roughly halfway through the period in question, 1998-2003 . I can recall lots of people I talked to were worried. In the same period I was giving talks and writing papers about the implications of positive lambda in LQG, partly because they are beautiful and partly to show that LQG could incorporate positive Lambda, while string theory could not. I always made that point in talks on the subject and was never challenged.

But, to answer your question with an example, lets use Witten, whose writing is pretty unambiguous. Here is more of the paragraphs I quoted in TTWP:

“However, an important no go theorem [6,7] says that there is no classical compacti cation of ten- or eleven-dimensional supergravity to de Sitter space of any dimension. This means that there is no classical way to get de Sitter space from string theory or M-theory. By a “classical” compacti cation, I would mean a family of compacti cations in which G (nΓ΄β¬β¬β¬2)=n becomes arbitrarily small and a supergravity or string theory description becomes arbitrarily good.

The no go theorem means that this does not exist.

In fact, classical or not, I don’t know any clear-cut way to get de Sitter space from string theory or M-theory. This last statement is not very surprising given the classical no go theorem. For, in view of the usual problems in stabilizing moduli, it is hard to get de Sitter space in a reliable fashion at the quantum level given that it does not arise classically. (For an analysis of a situation in which most moduli can be stabilized, leading in the large volume limit to a nonsupersymmetric vacuum with Lambda= 0, see [8].)

The absence of a classical de Sitter limit suggests that the possible values of N in string/M-theory are sporadic, rather than arising from in nite families, and that there might be only finitely many choices. If the number of choices is finite, I would not personally expect it to be possible to get N > 10^10^100. But de Sitter space with such large N is needed to agree with the most obvious interpretation of recent astronomical data.”

Now it turns out that at least at the semiclassical approximation KKLT work, Witten’s expectations appear to have been at least partly wrong, because N >> 10^500 seems to exist and to be sufficient. Of course, we don’t know whether there is a real consistent perturbative string theory past the semiclassical level of that calculation, so he could turn out to be right in the end.

I don’t know why so much is made of this, as to the extent to which this was a crisis for string theory, it was, at least at leading approximation solved by 2003, by the KKLT paper building on ideas and techniques Joe and others introduced. So this is a strory that comes out positively for string theory and the optimists among the string theorists. As I said before, I told the story to emphasize the implications of how the problem was so far solved.

Lets put it another way. The positive lambda string theory landscape was found in 2003. It has seriously puzzling implications. Were there another way to get positive lambda in string theory the crisis of the landscape might be avoided. But there is none known. Therefore there was no string theory compatible with positive lambda before 2003. But lambda was measured to be positive in 1998. Therefore there should have been a crisis.

The right thing to say,which is not what Joe is saying is, ‘we were very worried that the theory might be wrong, because it disagreed with data, and so we worked hard and solved the problem and saved the theory from otherwise having to be abandoned.” To the extent that string theorists want to claim there was no crisis in 1998-2003 they are implicitly claiming that disagreement with data is not a reason to suspect a theory is not true.

“Most embarrassing observation in physics Γ’β¬” that’s the only quick thing I can say about dark energy that’s also true.”

– Edward Witten, String Phenomenology 2005, Strings 2005, quoted in: http://www.itp.ac.cn/Download/spac2005/Kallosh-Beijing.ppt

(The observational evidence for a small positive CC is ambiguous because all that is seen is a lack of expected gravitational slowing of distant supernovae. According to GR, they should be slowing down at great distances, just as a bullet fired upwards will be slowed down by gravity. However, as Prof. Phil Anderson pointed out in a blog comment on Cosmic Variance, ‘… the flat universe is just not decelerating, it isn’t really accelerating …’ – in other words, the simplest explanation is that there ain’t any gravity force between receding masses over great distances. The reason for this lack of gravity is easy to explain with quantum gravity. The exchange of gravitons of some sort causes gravity. When the masses are receding, the received gravitons are redshifted, so they have less energy than the normally do,

E = hf.Lee,

It seems to me that we are still not entirely sure that the dark energy we observe is in fact a cosmologicgal constant with w = -1. It certainly looks like it is today, however in the period you mention this was far from clear. It could easily have been (and still might be) some form of quntiessence, which is why there was no ‘crisis’ in string theory over how to get a postive cc at that time.

Also, it should be mentioned that the basis of the existence of dark energy prior to 2002-2003 was the supernova observations. It was not really on completely firm ground until WMAP reported its results.

Dear Eric,

When you say, “It could easily have been (and still might be) some form of quntiessence, which is why there was no ‘crisis’ in string theory over how to get a postive cc at that time’ you seem to be implying that while there was no version of string theory before 2003 compatible with a constant positive vacuum energy, there were versions of string theory compatible with quintessence, which is a slowly changing but still positive vacuum energy. Is this right? If so, was there a prediction or expectation from string theory before 2003 for positive vacuum energy with some value of w besides -1? If so, then wouldn’t this still give an alternative to the landscape problem?

Thanks,

Lee

Lee,

My main point is that until the WMAP first year results, the problem of addressing the problem of dark energy was not seriously addressed. The KKLT solution came shortly thereafter. The difficulty in obtaining a cosmological constant in critical string theory was well-known and can be understood by considering the graviton beta function, which is just the Ricci tensor to lowest order. Conformal invariance requires that this beta function vanish, which implies a Ricci-flat solution to the vacuum Einstein equations. Thus, a cosmological constant is inconsistent with conformal invariance in strings.

However, there are linear dilaton backgrounds where problem of obtaining postive vacuum energy was solved. See for example, Antoniadis, Bachas, Ellis, and Nanopoulos:

1. Phys.Lett.B211:393,1988

2. Nucl.Phys.B328:117-139,1989

3. Phys.Lett.B257:278-284,1991

Best,

Eric

It was not really on completely firm ground until WMAP reported its results.I would say that some people are somewhat more skeptic (?)/ critical (?)/ pessimistic (?) than average. See the recent paper by Lieu:

http://arxiv.org/abs/0705.2462

(specially the tables).

Christine

Dear all, There was an interesting discussion on the topic of “A chain of reasoning is only as strong as its weakest step” over the “reference frame”, where LM offered a detailed critique on my point of view (also on other issues), but some comments there were more positive to it. (Of course, I am encouraged by Joe’s rather positive reaction to my point of view on this specific point.)

Dear Lee,

You keep claiming that there was no version of string theory before KKLT compatible with a constant positive vacuum energy.

I beg to differ:

hep-th/0106209 [84 HEP citations]

Silverstein: (A)Ds Backgrounds From Asymmetric Orientifolds

hep-th/0205316 [87 HEP citations]

Maloney: De Sitter Space In Noncritical String Theory

Eric:

So what new assumptions had to be made in ST in order for a positive CC to be viable?? Please try to be specific in lay terms. Thank you.

Dear Eric,

Please tell me if I recall correctly that linear dilaton backgrounds are conformally flat spacetimes, with a special choice of dilaton field linearly related to the time coordinate? If so, then these are very special backgrounds, and the fact that a positive vacuum energy in one frame may be possible did not lead to a solution to the real physical problem of finding a background that could be our universe. If I recall right there were also potential issues with instabilities also in these solutions. So the existence of a a few special and highly unphysical cases like these did not change the situation with regard to the problem of finding a potentially realistic vacuum.

Dear c,

I have basically the same question; I don’t have time to study again these papers, I did read them once, but 1) non-critical string theories, while interesting toys are unphysical and if I recall right there were also unphysical features of Silverstein’s construction.

Again, one would need an historian to do careful research to straighten out everyone’s recollections, but my memory is that untill the KKLT paper there was not believed to be a possibly viable string background that could describe a universe like ours, with a tiny but positive vacuum energy. But given that I don’t have now the time to study these papers, please tell us either that the solutions in these papers were and still are potentially realistic vacuum or tell us what unphysical feature they have.

Thanks,

Lee

Lee, here is my recollection, I don’t think we disagree on the facts, but probably on the phrasing. When the evidence for positive CC became overwhelming (though they were strong hints before) the situation in string theory was the following:

1. They were no known examples of string compactifications with positive CC, where everything was under computational control.

2. BUT, there was no statement (or reason) that there CANNOT be such vacua. In fact such vacua were constructed shortly thereafter by KKLT and others.

3. There was a no-go theorem (Maldacena-Nunez) showing that starting with higher dimensional theory, one cannot obtain deSitter vacua without invoking elements unique to string theory (e.g orientifolds). This statement is still correct…

In addition, I don’t remember anybody in that period (yourself included) claiming that string theory predicts non-positive CC, in papers or books or conferences or in person, quite possibly because that was untrue…

Lee,

I believe that linear dilaton backgrounds and non-critical string theory are one and the same. Sometimes this is called Liouville string theory or, more recently, supercritical string theory. The issue of whether or not any specific realistic worked out vacua have been discussed in the literature is not really relevant to the main point, which is that it was known before KKLT how to get a postive vacuum energy in string theory, which I believe now firmly established. I think that most of this work was in regards to inflation, rather than a solution to dark energy, as the existence of dark energy was not known at that time. More recent work has also been done.

Leaving the question, whether string theory was assumed to predict a non positive CC, to the historians, I as an outsider would be more interested, if the since then constructed string vacua with positive CC today look simple and natural or if they rather look artificial and far fetched. And here I would be most interested to have the opinion of Professor Polchinski first.

YES I would second Mike’s suggestion and add: What new assumptions had to be applied to ST in achieve a positive CC?. In lay terms would be very, very helpful. Thanks.

String theory never made a prediction that there couldn’t be a positive cosmological constant. The correct statement is simply that, for a long time, string theorists didn’t know how to compactify from ten dimensions down to four and obtain a positive cosmological constant. That could have been because there was no such way — and some people speculated about that, and wondered whether quintessence (which is not hard to get in string theory) could be responsible for the dark energy. Or it could simply have been because it was a hard problem, and nobody had put a lot of work into it, since most people thought the cosmological constant was zero.

As it turns out, it was the latter, as many people would have guessed. It’s a difficult problem, because getting a positive cosmological constant requires that we break supersymmetry, and that makes everything trickier, including stabilizing the moduli (pinning down the shape and size of the extra dimensions). But, faced with an unexpected experimental result, people did what scientists are supposed to do, which was to see whether it could be fit into their understanding, or whether they would have to change their theories in some way. As it happens, no alteration in the basic tenets of string theory was required; there are lots of ways to get a positive cosmological constant, sadly all too many.

If there is any deep lesson to be learned here, it’s not that string theorists refused to face up to the failure of their ideas — the ideas were fine, they just hadn’t been developed enough. The lesson is that it’s

really really hardto fully understand the physical implications of a rich theory in the absence of direct experimental clues.“If there is any deep lesson to be learned here, it’s not that string theorists refused to face up to the failure of their ideas Γ’β¬” the ideas were fine, they just hadn’t been developed enough. The lesson is that it’s really really hard to fully understand the physical implications of a rich theory in the absence of direct experimental clues.”

The definitive refusal to face up to failure occurred not before, but after KKLT, as some leading string theorists abandoned conventional scientific ethics, which require admitting failure when you are forced to keep making your theory more and more complicated in order to avoid contradiction with experiment, getting farther and farther from making a real prediction. Going on about how this is a success story, that the “the ideas are fine” or making excuses about a “rich theory” is just absurd. This is not in any sense an edifying story about scientific progress, but rather one that most particle theorists recognize as a deeply embarassing one. The effort being made on this blog to put lipstick on this pig is really misguided.

Peter,

At least questions such as the cc and particle physics CAN be addressed within string theory. That by itself is sufficient reason to study it. I do not believe that there is, at present, any other viable framework to study these problems (although I’m sure Lee will argue for LQG). If there is any failure, it is on the part of string theorists to completely understand the theory, not on string theory itself. As Sean points out, it is a very deep and rich theory, and the challenge to understand it completely is a diffiuclt one. However, my guess is that in the end, it will be worth the effort. Of course, we could just follow your path and not even try.

Eric,

I’ve never anywhere argued that people should stop trying to understand string theory. I am arguing that they should stop promoting as a success story something (KKLT and other moduli stablilization schemes) that is obviously a scientific failure and dead end. By doing this they are doing a lot of damage to the public perception of science. I really don’t think Sean, Joe, or the many varieties of Landscape (anthropic or otherwise) proponents have a clue as to how much damage this is causing. Going after Lee over this particular issue is a big mistake, since you’re ending up misguidedly promoting as a scientific success something which has been a huge failure and embarassment.

If you want to defend string theory against its critics, you should really think twice before taking your stand on the issue of the Landscape. It’s a completely indefensible position.

Peter, I doubt that anyone reading this far hasn’t heard our respective positions on this before, but nevertheless: I don’t really care whether the Landscape is a success story or not. I care whether it is true or false as a description of the world.

Gravity exists, and quantum mechanics exists. The correct theory of nature must be compatible with both of them. In the judgment of many people, string theory has a good chance to be that theory, or at least be a step toward the right theory. String theory seems to predict a landscape. If so, it may not be possible to make unique predictions for low-energy particle physics. Or it may be possible, via some correlations in the properties of different vacua or some cosmological selection principle. Right now we don’t know. One way or another, we are going to have to live with whatever is true. The universe doesn’t care whether we can predict the mass of the muon or not.

I’m not interested in defending string theory, telling happy stories, or forcing the universe to conform to my wishes. I just want to do my best to understand nature and tell the truth about it. If the public is interested in following what we’re doing, whatever tentative state our understanding might be in, I’m happy to do my best to explain it. Whether our current ideas are right or wrong, time will tell.

Peter,

In addition to agreeing with what Sean said, I don’t think that I have made any arguments in favor of the landscape. My personal opinion on this is that there will be discovered some vacuum selection principle once we have a fully non-perturbative formulation. Right now, we just don’t have the tools to answer this question, and we won’t unless people work to develop them.

Dear Eric,

The problem i have with your statement, ‘My personal opinion on this is that there will be discovered some vacuum selection principle once we have a fully non-perturbative formulation.” is that people have been saying this since it was clear there was a vast landscape of solutions in 1986. Then came the “second revolution” based on duality and branes which give, if not a fully non-perturbative formulation, at least the ability to calculate in some cases non-perturbative effects. The result was that things did not get better, they got much worse. First, because we could argue from S duality that many of the supersymmetric vacua that are stable at weak coupling are also stable at strong coupling. Prior to that there were many hopes that non-perturbative effects would destabalize the supersymmetric vacua. Now we know that whatever else happens, there is a vast landscape of supersymmetric vacua stable at both strong and weak coupling. This greatly limits the scope of any dynamical vacuum selection principle, because it will not explain why the world is not in one of the vast number of stable supersymmetric vacua.

Then, when fluxes and branes played the key role in stabilizing the moduli and getting us positive lambda, the role of non-perturbative effects was to make the landscape problem worse again. The no go results say that there are no compactifications down to deSitter classically, but when non-perturbative effects are added there are now another vast catelogue of solutions.

So, the trend is that non-perturbative effects make the landscape problem worse, not better. So is there a way out? One is to put a bit more effort into other ways to quantize gravity and unify the interations that may not have a landscape problem. One is to try to reinvent string theory a fresh, completely non-perturbatively. One is to invent approaches to the landscape that do lead to falsifiable predictions-and the only one ever proposed is cosmological natural selection.

Would you not agree that either or all of these three options are more likely to succeed than to continue straight ahead applying to the landscape strategies based on the anthropic principle that have been shown by straightforward logical reasoning to have no chance of leading to falsifiable predictions? If so, then why are string theorists putting much more effort into this than into any of the three options i mentioned?

Thanks,

Lee

Lee,

My statement was that we’ll probably only understood why a particular vacuum is selected when there is a completely non-perturbative formulation, not just adding non-perturbative effects. One could always try to formulate such a theory from first principles; however, I believe the approach that is taken is to work backwards from perturbative string theory. If it’s possible to find a vacuum (or vacua) that reproduces known particle physics, has a positive vacuum energy, and all moduli are stabilized, then this may provide clues to the completely nonperturbative theory. The problem with trying to do this from first principles is that we don’t really know what the principles should be or what this theory should look like. We just know it’s perturbative corners. Perhaps other approaches such as LQG will eventually shed light on this, but in all liklihood string theory will still be part of the picture. So, people should work on what they find interesting and where they can make progress. I don’t know why there needs to be this polarization with respect to string theory and other approaches to quantum gravity.

Eric

Sean – Please to know you have such an open healthy attitude in 72.

Eric – Is it clear (perhaps except to you) that you are desperately holding on to well-tried approaches. I too first heard of the vacuum selection principle some 20 years ago. The fact that none is found is one reason behind the big trouble with ST. For a long time I believed in much of ST. Today, I don’t believe there is such thing as 1-d string, period. The universe is not 10/11-d, although I am still open to 4+1d (and some form of brane concept but not the current one). Therefore, there is no need for any vacuum selection principle. As D Gross said there is something very fundamental missing in our picture. To me, the biggest contribution of ST to physics is showing convincingly that its basic assumptions, postulates, conjectures, and finding are all wrong as a physical theory. (But certainly a lot of the nuts-and-bolts could be useful down the road.)

A few little points:

1. A claim that Peter is making along the discussion which is of interest is that current string theoretic models being more and more complicated is an indication that the theory is heading in the wrong direction or that it failed. I think it is an interesting issue how such a claim can at all be discussed and examined (and even if it can be examined at all.) It can well be argued that more and more complicated models are quite expected also in a successful development of a scientific area. Anyway it is an interesting issue.

2. ML (the owner of ‘the reference frame’) raised an interesting point that the overall assessment of string theory is too ambitious project to be scientifically fruitful. (Mentioning ML’s full name will cause the comment to be blocked.) I think there is some truth in this claim as indeed the overall assessment of ST is well beyond the horizon. (Sean’s remark #72 expresses a similar idea.) Sometimes, miraculously, studying mundane matters changes dramatically the horizons of knowledge but discussing matters well beyond the horizon while of interest is often not so scientifically fruitful.

3. The issue of rigor and the points that Joe raised regarding it (as the strong counter points by Hendrik) are certainly interesting and important. I realized what was the thing that disturbed me about Joe’s comments concerning rigor. It is actually the rhetoric more than the substance. In the scale between useful and useless (which has a lot of grey colors) there is no such thing as “worse than useless”. Similarly, in the scale between right and wrong (also with a lot of greys) there is not really a place for “not even wrong”.

The physicists endeavor of quantum gravity as the mathematicians journey for mathematical rigor of the foundations of physics cannot really be tagged as “useful” in the ordinary usage of the word ‘useful’. (Compared, e.g. to the usefulness of garlic.) Some mutual empathy can be useful. (And potentially each of these two endeavors can occasionally offer useful insights to the other.)

4. If I can recommend to you a useful and beautiful academic area which has connections with and applications to all of the exact sciences as well as practically all areas of social science and some areas of humanities, which also has important connections to many real life problems (and not the least, baseball) and to engineering, which is related to a lot of mathematics, both deep and simple both rigorous and heuristic, and to profound calculations; an area with subtle and controversial foundations, glorious history, with a few uphill struggles for recognition; an area offering difficult ethical and moral dilemmas, and if I may say so, an area with a brilliant future: This is the area of

statistics.Invcit #39:

When cosmologists started studying inflation in the 80’s, they found that in many models the universe would inflate to much greater than what we can see – there would be many `universes’ – and that different parts would have different laws of physics. Andrei Linde in particular argued that this is the way things are. If the landscape is right, then in string theory this is true in a big way. So we have to understand the `many worlds’ of this picture as we have understood the `many worlds’ of QM. The most exciting outcome would be if these were related. A selection of recent papers can be found at http://www.slac.stanford.edu/spires/find/hep/www?rawcmd=FIND+ti+eternal+inflation&FORMAT=www&SEQUENCE=

Hendrik #35 and Gina #32:

I agree that I am going a little too far on this rigor thing. This is partly a response to Lee’s going way too far in the other direction, but also partly a reaction to my own misspent youth. I used to focus too much on rigor and formalism, and have become a much more creative and productive scientist since learning, very slowly, to see through these to the physics. Hendrik – if you can tell me, in a non-technical way, what Dimock, Wiesbrock, and/or Rehren have shown, it would be interesting and I will respond if have anything useful to say. I agree that there are some elegant and enlightening proofs, especially in statistical mechanics, but there are also examples like the continuum limit of Yang-Mills in 4 dimensions, which is a standard calculation in a quantum field theory course (asymptotic freedom), but took Tadeusz Balaban over 300 pages in Comm. Math. Phys. to make mathematically rigorous. So this is why I say that what we can understand physically much more than we can prove.

Mike #67 Cecil #68:

“Do the string vacua with positive CC today look simple and natural or if they rather look artificial and far fetched? What new assumptions had to be applied to ST in achieve a positive CC?”

There is a general principle in physics, that we expect the equations to be simple (and beautiful, if that means anything), but that the solutions can be very complicated. This is after all the way science works, that we explain diverse phenomena in terms of simple equations. The world we see is certainly very complicated, with varied structures on many scales, and even microscopically most of the symmetry of the equations is broken. So by this measure the string vacua that we are discussing are not especially complex.

You might ask another question: we might expect that the universe had a simple initial condition – could these complicated solutions have actually been realized? Looking for example at the most-discussed model of initial conditions, the Hartle-Hawking `no-boundary’ proposal, this gives rise to complicated vacua as easily as simple ones, there is no penalty for complexity.

The history, as one might expect, has been to understand the simple solutions first and then work towards more complicated ones. When solutions of the necessary complexity (broken supersymmetry) were reached, e.g. Silverstein 2001 and KKLT 2003, positive and negative cc’s were both there. It seems like a successful scientific process, Smolin’s claims of crises, ethical failings, and wrong predictions notwithstanding.

Lee:

Three points:

First, regarding the false prediction: As Sean points out at length, there is a world of difference between `X has not been shown’ and `Not-X is predicted.’ Now you change the subject to the former, but in your book you have told a detailed, specific, and compelling story of the latter. Amos and many others have found this to be “the most persuasive thing in the book,” and yet it is sheer fiction. To repeat: my review pointed out that your story was manifestly inconsistent with the history of string theory; you came back in your response with an explanation that made no logical sense; now you blame differing memories,

change the subject, and express annoyance at having your facts challenged.

Second, regarding your assertion, that the evidence supports a weak form of the Maldacena conjecture: arguably this is one of the most important points of science in the book, since it relates to string theory’s claim to be a non-perturbative construction of quantum gravity. Therefore it is reasonable to assume that your words “a weak form of the Maldacena conjecture” actually have some definite meaning. I know that your book does not cite your paper with Arnsdorf, you have not cited any scientific papers at all here. So I have gone to your various scientific papers in which you compare the status of different theories of quantum gravity, and the paper with Arnsdorf is the primary reference on this point. If this is withdrawn, not much if anything is left. I have found another “weak form” definition in your book, as I have noted, but this is tantamount to a full theory of quantum gravity, so it is not very weak at all. Now you say that you

“do suspect that there is a weaker conjecture that is consistent with all evidence, let me come back to that sometime when I have time to think it over carefully.” One would have expected that you would have thought it over when you made the original statement.

By the way, I think that you are wrong about where your paper with Arnsdorf went astray (unless in more than one point) – I believe that it was in inconsistent interpretations of the expression “fixed causal structure.” But if you are correct, that the problem is a limitation of the applicability of Rehren duality, then it must fail in any interacting QFT (because the interaction always produces refraction, which your argument forbids): this would imply that Rehren duality can hold only in free field theory. This would confirm my overall point of view, that it is easy to prove trivial things, and much harder to prove things that are physically interesting.

Third, regarding sociology: You say

Apologies, I hit `submit’ before fixing my formatting at the end:

This is exactly what you have done, and I have already pointed out where…

Yes, I know this, and it is why I am so perturbed to find my discussion of the existence of the CFT placed in this part, and characterized as a sociological argument, and a prime example of groupthink. The construction of quantum field theories is a deeply scientific subject to me, and one that I have given great thought. You may disagree with me (though I am rather certain that I have the science right here), but to dismiss this scientific issue as sociology and groupthink is outrageous. I find it particularly outrageous because many members of the public, and even some scientists in other areas, have accepted your claims throughout the book with remarkable credulity. Hence the effort I am making here.

To summarize, I am not picking nits here, but focussing on some of the most important points: your central historical story, one of the central pieces of physics, and a major sociological argument (and one that refers to me directly); however, this kind of exaggeration and manipulation of the facts runs throughout the book.

Smolin’s chapter 16 discuss a lot of interesting physics before proceeding to the (less interesting, in my opinion) sociology. So it can be regarded as prestigious to be mentioned also in this chapter along with Maldacena, Mandelstam, Witten and others. Lee’s specific point is not convincing. Horowitz and Polchinski compared AdS/CFT to the Riemann hypothesis as being in the category “true but unproven”. This is a nice analogy which can be flattering to everybody. Lee’s specific point is that the Riemann hypothesis is a conjectured relation between two structures that exist mathematically. Somehow I do not think Lee’s distinction makes a lot of difference and I would not be surprised if there are important conjectures in the area of mathematics about relations between two structures which are not known to exist mathematically, and their mere existence is part of the conjecture. Anyway, my impression is that AdS/CFT for string theory is like the smile for the famous cat, which is present even when the cat itself cannot be seen. And maybe it holds a key for rigor as well.

Joe wrote about his attitude towards rigor that it is ” also partly a reaction to my own misspent youth. I used to focus too much on rigor and formalism, and have become a much more creative and productive scientist since learning, very slowly, to see through these to the physics.”

It is always interesting and moving to see people reflecting on their youth. Let me suggest that the years spent on rigor and formalism were not wasted, not only because rigor and formalism are important scientific values, but also because “learning very slowly to see through these to physics”

correctly, may well depended on those years of struggle with them. It will be interesting to see Joe’s further reflection on this, say, in 2027.Sean,

“One way or another, we are going to have to live with whatever is true. The universe doesn’t care whether we can predict the mass of the muon or not.”

The problem with the landscape is not that it doesn’t allow us to predict the muon mass but that it doesn’t allow us to predict anything at all. There is zero evidence for the kind of “correlations” you mention: no reason for them to be there, and people who have done calculations looking for them haven’t found anything useful. Similarly for a “cosmological selection principle”.

Yes, we have to live with whatever truth the scientific method turns up. But what is going on here is not the scientific method. Instead we’re being sold a “theory” that can’t predict anything because a lot of people refuse to admit it has failed. This is not normal science.

Dear Eric,

I spent many years working on formulating a completely non-perturbative formulation of string/M theory, I have a strategy, which has led to some results (certainly non-rigorous). Here are some of the papers where these results were presented. hep-th/0003285, hep-th/0006137.hep-th/0002009, hep-th/0104050 (which I am most proud of), hep-th/0503140. Since you think this problem is the key to the landscape crisis I would hope you are working on it, I would be curious if you want to share your strategy and results.

On polarization, I don’t think there needs to be a polarization and it would be much healthier for science if there was none, which would mean that all approaches to quantum gravity would be considered the same general field, with people typically working on different approaches and being in research groups with people in other approaches, going to the same conferences etc. This is how we work in the quantum gravity world and we have often reached out to the string theorists to include them in our conferences and to support hiring them to balance our departments, institutes and research groups. I am not the only person in this world who has worked also on string theory and there are also instances, some very recent, in which people in LQG advocated or supported hiring string theorists. The polarization comes from people who want to promote one approach to a field of its own that works in isolation from the others, who do not reciprocate this openess and inclusiveness to approaches not their own.

To Joe and others,

I will try to reply in more detail later, but I am traveling for most of the next two weeks. So I will address only the “false prediction” issue. First, note that the wording on 153-5 is careful and shows some nuance. I emphasize “I don’t know of any particular string theorist who predicted that the cc could not be a positive number, but…” “Indeed there were theorems …AT LEAST AS LONG AS QUANTUM EFFECTS WERE NEGLECTED…” which is a fair characterization of Witten’s comments, from which I next quote. and then I stress, “In this case the optimists were correct.” I don’t think your comments do justice to the care and nuance here.

But I am also happy to say that were I revising the book I would stress that there were different views between 98 and 03 about whether the problem of making a string theory with a positive but tiny cc was a crisis or not. I have learned some things from this discussion which would certainly lead to a still more nuanced telling of this part of the story. However, I do not agree that there was no sense that this was an issue, because I have vivid memories of discussions with people who shared a sense of crisis over this issue.

Thanks,

Lee

Dear Professor Polchinski,

your answer about string vacua made sense to me. In my words:

The equations are simple, solutions may be complicated, this is, how good physics has always been so far. After all, the complexity of the world, we see around us, has to go somewhere. As you said, the better question to ask is probably, can those string vacua with positive CC occur naturally given the best cosmologic theories we have today. And I understand, the answer is yes, equally well as some simple string vacua.

May I bother you with another question?

What worries me, is, what Sean says:

“The universe doesn’t care whether we can predict the mass of the muon or not.”

To me it does not seem to be an indication of great optimism for string theory, that Sean mentions, what we might not be able to calculate without mentioning, what we are hoping to calculate, be it tomorrow or one day in the future. May I ask you, what you hope to calculate from string theory? As far as I understand, the theory has a huge space of adjustable parameters, so don’t we need a lot of predicitions (or maybe postdictions) to balance that? Is there hope to arrive at a string vacuum reproducing the particle spectrum we know about plus predicting some new particles, we will then see with our newest collider?

Mike,

String vacua are not trying to reproduce the complexity of the world, just the complexity of the SM Lagrangian, which is not very complicated. Actually, as far as I can tell, the equations that determine string vacua aren’t any simpler than those of the SM Lagrangian. What is going on here is not normal physics.

Good luck getting Sean or anyone else to tell you what predictions they expect to get out of the landscape. There are currently no landscape predictions about what the LHC will see, nor any reasonable hopes for getting any.

The Standard Model is pretty complicated. It’s based on the gauge group SU(3) X SU(2) X U(1), with three different gauge coupling constants, and with left-handed Weyl fields in 3 copies of tthe representation (3,2,+1/6)+(3bar,1,+1/3)+(3bar,1,-2/3)+(1,2,-1/2)+(1,1,+1), and a complex scalar field in the representation (1,2,-1/2). All Yukawa couplings allowed by the gauge symmetry must be included; this allows for three different 3×3 complex matrices of Yukawa couplings (though many phases can be absorbed by field redefinitions, leaving 13 parameters to be specified: 9 eigenvalues and 4 mixing/phase angles). The eigenvalues range over 6 orders of magnitude. No one knows why.

And all this yields exactly massless neutrinos. Neutrino masses require more fields and more parameters.

It’s not going to be easy for some extremely elegant theory to reproduce this mess. In fact, I know of no example in physics where an elegant theory has a big mess as the UNIQUE solution. On the other hand, it’s often possible to get a landscape of MANY DIFFERENT complicated solutions to nice equations (e.g., molecular dynamics). To me, the big sociological mystery is why we ever thought it was going to be different this time.

Mark,

The SM choice of gauge groups (U(1), SU(2), SU(3)) a list of 3 of the simplest Lie groups, the representations of the fermions are all in the simplest defining rep. The only thing about this which is slightly complicated is the U(1) hypercharge assignments. What is more complicated is the Higgs sector, the part of the SM we’re not happy with anyway. Almost all of the SM parameters are the Higgs Yukawas.

But “complexity” is a relative notion, and you’re completely ignoring my claim that the equations one has to solve in order to find the “vacuum state” corresponding to our world are at least as complicated if not more so than the ones that define the String theorists are misleadingly claiming to have a simple set of equations whose solution reproduces the “complicated” standard model. This just is not true. If you disagree, please show us explicitly the set of equations, over which variables, whose solutions give a fully stabilized vacuum state of a string theory whose low-energy limit looks more or less like the SM.

in previous comment there’s a “SM” missing, in “if not more so than the ones that define the SM.”

Peter claims: ” the equations one has to solve in order to find the “vacuum state” corresponding to our world are at least as complicated if not more so than the ones that define the SM”

So what? Are these equations required to be simpler? Is such a simplification always the case when a large, deeper, and more comprehensive physics theory includes an earlier theory of much more limited scope?

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I donΓΒ΄t know about everybody else, but in my browser comments below some point appear cut on the left margin. If that is a problem on the cosmic variance site I’d wish it could be fixed, as i is too bad to be unable to follow this very interesting discussion.

I would consider the explanation via quantum mechanics of the periodic table of elements to be elegant and simple (even though the detail is complicated). The entire “landscape” of chemistry and biology follows (in principle) from the same explanation. Yet it is not a landscape in the string theory sense, because there is a uniqueness to the explanation, we just cannot compute it. There are not twenty versions of water. I do call it a landscape because our ability to make pro-active predictions is rather limited (given physics one cannot predict the DNA molecule), but given a (chemistry) phenomenon, we can provide an explanation in terms of the constituent parts (given physics one can construct a useful account of the DNA molecule.)

String theory does not shine in any of these types of explanations.

More complex mathematical models for the physical world are justified if there is a pay-back in terms of solid predictions which can validate the need for the additional complexity. The nemesis of physics is the endlessly complex theory which makes no falsifiable predictions and is proudly defended for being incomplete.

Ockham’s razor (entia non sunt multiplicanda praeter necessitatem): “Entities should not be multiplied beyond necessity”.

String theory multiplies entities without necessity. Where is the necessity for anything in string? If there is no falsifiable prediction, there is no necessity.

Don’t get me wrong: I’m all for complex theories when there is a pay-back for the additional complexity. In certain ways, Kepler’s elliptical orbits were more ‘complex’ than the circular orbits of both Ptolemy and Copernicus, oxidation is more complex than phlogiston, and caloric was replaced by two theories to explain heat: kinetic theory of gases, and radiation.

These increases in complexity didn’t violate Ockham’s razor because they were needed. Maxwell’s aether violated Ockham’s razor because it required moving matter to be contracted in the direction of motion (FitzGerald contraction) in order for the Michelson-Morley experiment to be explained. This was an

ad hocadjustment, and aether had to be abandoned becaus it did not make falsifiable predictions. Notice that Aether was the leading mathematical physics theory of its heyday, circa 1865 when Maxwell’s equations based on the theory were published.String theory has not even led to anything predictive like Maxwell’s equations. String theorists should please just try to understand that, until they get a piece of solid evidence that the world is stringy, they should stop publishing totally speculative papers which saturate the journals with one form of speculative, uncheckable orthodoxy which makes it impossible for others to get checkable ideas published and on to arxiv. (Example: Sent: 02/01/03 17:47 Subject: Your_manuscript LZ8276 Cook {gravity unification proof} Physical Review Letters does not, in general, publish papers on alternatives to currently accepted theories…. Yours sincerely, Stanley G. Brown, Editor, Physical Review Letters.)

Publius, it happens for me (margins clipped) only with Internet Explorer. As some would say, find a real browser, like Firefox.

My problem with the margins disappeared when I upgraded from IE6 to IE7, which is freely available from M$.

Dear Prof. Polchinski, regarding the side issue of rigor:-

This is not my favourite piece of mathematical physics either;- I am not so convinced by the approach of lattice QFT. This illustrates a central problem for mathematical physics, in that the same piece of physics may have many different ways of being made rigorous. The physics produces a set of structures in an ill-defined framework, so there may be several rigorous frameworks in which the physics structures can be realized. Nevertheless, this work needs to be done in order to analyze the physics structure properly, and to find the most appropriate formal framework for the physics.

I agree that we lag very far behind in making established physics rigorous,- the burning example is of course the standard model (or even its component theories e.g. quantum gauge theory). As physics, the standard model functions pretty well without any rigour. But we do not fully understand it until it has been made rigorous (and hence cannot extrapolate it confidently into new areas). Establishing a rigorous standard model is still a work in progress, although already a great deal has been learned from analyzing some of its components.

A bit of a tall order, but since the original claim was that string theory can benefit from the rigorous approaches, I’ll write something in this general area. Formally, the (free open bosonic) string is defined as an infinite collection of quantum oscillators together with a set of gauge transformations (generated by constraints). This abstract structure can easily be encoded in terms of a C*-algebra with the action of the group of gauge transformations on it (cf. Commun. Math. Phys. 156, 473-525 (1993)). Now in the usual approach to strings the algebraic structure of strings is realized (quantized) as operators (a) on Fock space, and (b) with a normal ordering convention. This creates two problems: first, the constraints acquire a central term (anomaly) which makes them second class, hence they cannot be satisfied. Second, the Fock complex structure is not left invariant by the gauge transformations. These problems lead then to a range of further choices, e.g. a maximally commutative set of constraints is selected and imposed as `weak’ constraints. Since these still do not have a solution due to continuous spectrum problems, a Gupta-Bleuler method of imposition is taken, and this leads to the dimension 26 requirement for positivity of the final space. These problems can be circumvented by a different choice of representation of the original algebraic system. Such representations are available to you because this is an infinite dimensional canonical system. Even if one takes the reduced set of constraints, one can avoid Gupta-Bleuler (and indefinite metric) by selecting other representations in which the constraint condition makes sense (see the paper http://arxiv.org/abs/math-ph/9812022 for this). I suspect that the dimension 26 requirement is purely due to the incompatibility between the Fock representation and the gauge transformations. Even Mickelsson found this requirement early in Commun. Math. Phys. 112, 653-661 (1987) when he took the orbit of Fock structures generated by gauge transformations and considered Diff S^1-invariant sections of the bundle of Fock spaces. So, if one abandons the Fock representation, I think the dimension 26 restriction may be lifted.

(My apologies for the references to my own papers above;- it is just that I know their contents the best).

Dimock has a few papers on strings, in e.g. http://arxiv.org/abs/math-ph/0102027v1 he constructs a rigorous covariant free bosonic string as an operator theory (this is not new, it is already in Commun. Math. Phys. 156, 473-525 (1993)). The constraints cannot be satisfied due to continuous spectrum problems, so, to satisfy them he picks out certain components of an integral decomposition of his Hilbert space which implies a mass quantization for the string. As for Wiesbrock, he takes an idea of Witten in Nucl. Phys. B 268, 253 (1986) that for interacting strings the splitting and joinings define a groupoid structure. In Commun. Math. Phys. 136, 369-397 (1991) Wiesbrock constructs a C*-algebra which carries all the representations of this groupoid. A review of this paper is at Commun. Math. Phys. 156, 522-525 (1993). Rehren has a more descriptive paper of his work at http://arxiv.org/abs/hep-th/9910074v1.

“As physics, the standard model functions pretty well without any rigour. But we do not fully understand it until it has been made rigorous (and hence cannot extrapolate it confidently into new areas).”

I do not understand how you can make such a statement. The Standard Model breaks down at the scale at which the Higgs self interaction develops a Landau pole. No amount of mathematical rigour is going to help you “extrapolate it confidently” into the energies above that.

So, if one abandons the Fock representation, I think the dimension 26 restriction may be lifted.Bad idea. It is an experimental fact that energy is bounded from below. Hence you need representations of lowest-energy type!

It is an important but not very widely known fact that conformal anomalies have been observed experimentally, at least in computer experiments. The free energy per unit length in a infinitely long strip of width L acquires a universal correction proportional to c/L, and this prediction has been confirmed. More generally, the central charge couples to length scales, e.g. the cosmological constant.

I suspect that the dimension 26 requirement is purely due to the incompatibility between the Fock representation and the gauge transformations.Anomalies have a beautiful geometric interpretation. I don’t understand how some algebraic understanding of field theory could vitiate this understanding and magically cause anomalies to disappear.

96 invcit

If the initial assumptions of the SM are made clear, and it is rigorously constructed (hence without contradictions) then it cannot “break down” in a logical sense. So it can be applied wherever its assumptions hold, which is what I meant by “extrapolate it confidently”. It becomes then a purely experimental matter to determine its domain of physical applicability.

———————–

97 Thomas Larsson on Jun 3rd, 2007 at 9:13 am

An “experimental” fact can only give you a requirement on your final physical system i.e. after constraining is done, not before. So the defining representation has a lot of freedom in it. In fact, in our treatment of Gupta-Bleuler in http://arxiv.org/abs/math-ph/9812022 we did obtain Fock representations on the final physical algebra, but the important fact is that these representations did NOT come from an initial Fock representation.

—————–

98 Aaron Bergman on Jun 3rd, 2007 at 9:19 am

A bit hard to answer in this generality;- If you look at the Carey-Ruijsenaars paper, anomalies are there obtained by the twist of quasi-free second quantization. These anomalies definitely need not appear in other representations.

Sorry, nested blockquotes didn’t work;- here’s a better rendition of my response to Thomas Larsson above:

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97 Thomas Larsson on Jun 3rd, 2007 at 9:13 am

An “experimental” fact can only give you a requirement on your final physical system i.e. after constraining is done, not before. So the defining representation has a lot of freedom in it. In fact, in our treatment of Gupta-Bleuler in http://arxiv.org/abs/math-ph/9812022 we did obtain Fock representations on the final physical algebra, but the important fact is that these representations did NOT come from an initial Fock representation.

My understanding comes from the experimentally proven application of CFT to statphys. The relevant Hilbert spaces (minimal models) are not Fock spaces, but there is an energy bounded from below, and that’s what gives rise to anomalies. In the physical Hilbert spaces; there is no constraining to do (apart from factoring out two singular vectors), because the anomaly converts the classical conformal gauge symmetry into a quantum global symmetry.

The situation is similar for the free subcritical string. The classical theory has a gauge symmetry, which becomes global on the quantum level because some gauge dofs (trace of the metric) become physical. Conversely, these dofs decouple in the classical limit, making the system a classical gauge theory. This is compatible with unitarity.

92 Nigel

Hi Nigel,

I think, what you say, is very important.

Maybe we can come to an even more precise statement, if we define, what “complexity” and “predictivity” mean.

I suggest to define “complexity” as the effort needed to understand a theory and then to calculate something from it. On the other hand, a theory is more “predictive”, when it describes a broader or at least equally broad scope of phenomena with less adjustable parameters.

This means we want a simple or less complex theory, because we are “lazy” (or because we want more “physical inside”). For being physicists we want a predictive theory, but it is clear, that there can be trade off between complexity, number of adjustable parameters and scope. (And for being humans we want a beautiful theory.)

In this view, string theory is currently in the red corner of all three dimensions:

10^500 adjustable parameters, no (quantitative) predictions and complex as hell.

A string theorist would probably argue, that this is, because the theory is work in progress and of course, this being fundamental research, he/she and nobody else can predict for sure, if and when such a progress will me made. If I understand him right, this is, what Smolin then means by “scientific judgement”, and every active scientist in the field has to make this for himself. And if you are not an expert yourself, then you have, as always, to decide, whose judgement you believe most. But at least, we can be clear about the open status of string theory today.

Well, my understanding comes from quantum constraint theory. The system here under discussion (free open bosonic string) is exactly defined by imposing constraints on an infinite set of quantum oscillators. So for this system there definitely is nontrivial constraining to do, and hence one should only require something physical like a positive energy on the final system not the original one.

To give you an indication of how much freedom this gives you;- in the C*-algebra approach we deal with global (integrated) quantities, hence with the gauge transformation group (not the infinitesimal generators). So a larger set of representations of the gauge group is now available, e.g. those which are not continuous in some directions. If there are constraints, one does not need to require continuity on nonphysical objects, so this is not a problem. In fact, in our version of Gupta-Bleuler electromagnetism quoted in my previous post, we did find that the physical representations had to be discontinuous on nonphysical objects (nonregular representations). Maybe this is the resolution for the representation facts which you refer to from CFT, insofar as those facts perhaps pertain to continuous (projective) representations of the diffeomorphism group of the circle.

You are of course free to define whatever you like, but the quantization of a classical gauge theory does not need to be a quantum gauge theory. It is obviously true that the constraints can only be imposed when D = 26, but the no-ghost theorem asserts that the unconstrained Hilbert space has a postive-definite inner product when D < 26, cf. GSW chapter 2. This may hence be viewed as the quantized subcritical string. The anomaly turns the classical gauge theory into a quantum global symmetry.

I don’t think so;- this definition of the string is the old one you find in Scherck and in the introduction of most string books.

I cannot make much sense of this clause;- for a start, quantization is not a well-defined map from the classical to the quantum theory; there are serious existence and uniqueness problems (cf. http://arxiv.org/abs/dg-ga/9605001). I presume you mean that the quantum constraints which you define have an anomaly i.e. are second-class. But as I pointed out before, a different choice of representation may allow you to avoid this. By the way, second-class quantum constraints can also be imposed (algebraically, not as state conditions) cf. Comm. Math. Phys. 119 (1988), no. 1, 75-93, so there is another alternative as well.

I think we are going in circles;- this was the starting point of this strand of the debate, where I suggested that one can avoid this by abandoning the Fock rep.

Dear all,

1. Regarding Nigel’s interesting comment (#92),

I thought that Peter’s point (#86) can be discussed as a separate issue from the issue of predictions. As for predictions, Joe explained it very nicely in his first reply. Indeed it appears to be agreed that the issue of predictions is a weak link for the string theoretic understanding/view of our universe. (And it will probably be a weak link for any alternative point of view.)

Apropos predictions it may be helpful to try to draw some lines between scientific predictions, scientific hopes, and scientific prophecies. While the borders are not always clear these three are quite different. (And all three can be of interest, value and even fun.)

Peter’s question reflects the scientific hope that the equations for SM within string theory (or any other theory of quantum gravity) will be simpler than for the SM standing alone. This may lead to some explanation for aspects of the SM which looks arbitrary, and perhaps to further understanding and some predictions within the scope of the SM as well. There is nothing wrong with this hope. It is a nice hope, and quite possibly one of the motivating hopes for string theory. (Indeed, also in Peter Shor’s amusing Amazon review of Smolin’s book that Joe mentioned this hope is described as a central motivation for ST.)

As nice as this hope is, attacking ST on the ground that it does not meet (yet or even ever) this particular hope is not convincing. Not explaining the parameters of the SM is not an obstacle for ST to explain things beyond the SM and to become a theory of quantum gravity that accommodates the standard model. Achieving this will already be a scientific landmark of the highest quality and magnitude.

String theory (but possibly also competing theories of quantum gravity that include the standard model if and when such theories will emerge,) may offer an explanation for the parameters of the SM, as representing a sort of typical or random instance of the theory, perhaps conditioned, on some basic properties of our universe. Such an explanation (and even its scientific legitimacy) is very controversial within the ST community and outside it. (Personally, such an explanation does not strike me as non-scientific.)

Another aspect of Nigel’s comment which I find problematic is that it seems that Nigel suggests a sort of definite a priori “Litmus test” for emerging scientific theories. This does not sound realistic.

Regarding Nigel’s PRL (subjective) ordeal may I say that one of the nice things about many human activities (like the academic endeavor) is the possibility to see importance and find meaning in matters that from the outside seems utterly unimportant and quite meaningless. One of the drawbacks of this nice feature is that sometimes mundane matters (like a rejection of a paper or a book) seem far too important and far too meaningful.

2. Regarding positive cc.

I do not think Joe’s and Lee’s description of the history are so different. It is agreed that positive cc was a surprise, and it is agreed that ST can accommodate positive cc. Joe views the positive cc as a place where perhaps string theory “already makes connection with observation,” and Lee regards this story perhaps as an indication how ST can accommodate anything and interprets it negatively.

(Lee’s point of view is complex. In #43,#53 Lee mentioned that the ST solution to positive cc was a success and remarked that Joe’s optimism turned out to be correct. Woit (#72) regards it as “obviously a failure and a dead end”. Clearly, the word “obviously” cannot apply to a matter where even Lee disagrees with Peter.)

In any case, both Joe’s and Lee’s interpretation are consistent with their prior approaches to the matter at hand and both do not contribute much to establish these prior approaches.

The positive cc story demonstrates a weakness of the falsifiability argument against string theory. Lee was pessimistic about the possibility that string theory can accommodates positive cc. Had it turned out that string theory cannot accommodate positive cc this would have falsified the theory.

3. Regarding Clifford pingback (#89).

Let me comment that while Clifford is my world-wide favorite blogger, his description of Joe’s second reply as: “the latest installment of Joe Polchinski’s rather thorough deconstruction of the nonsense, obfuscation, selective memory, and other confusions that constitute the bulk of Lee Smolin’s attack on string theory,” does not come across as correct or fair. (What is nice about Joe’s approach is that he is trying to discuss the most interesting scientific aspects and not necessarily the weakest links in Lee’s book.)

Clifford is correct, I think, in viewing the titles of Sean’s posts as somewhat peculiar; while Sean supports the ST endeavor the titles of the two recent posts seem (unintentionally) damaging to the ST side of the “public debate”.

4. Regarding Hendrik’s interesting comment.

Among other things Hendrik suggested: “So, if one abandons the Fock representation, I think the dimension 26 restriction may be lifted.”

This looks like a nice scientific hope, (albeit seemingly far-fetched). Do you have, dear Hendrick, any evidence (rigorous or non rigorous) to support this hope? Also, wouldn’t you agree that for pursuing such an idea, it will be more efficient to still use physics’ more relaxed rigor standards rather than full mathematician’s standards of rigor?

Do you expect, Hendrick, that abandoning “Fock representation” will allow to work in any dimension and the 26 dimension restricting will be entirely lifted? Or perhaps you expect that the dimension that will burn the anomalies will depend on some parameter of your hypothetical theory, like the cc.

It is interesting that for some layperson the universe having many hidden dimensions is very appealing while for some it is a very disturbing idea. Moving from four dimensions to ten or eleven looks dramatic but does not look nearly as dramatic as QM’s dices. For me, the many dimensions is an appealing aspect of string theory (but perhaps a little arbitrary).

It is a difference in desiderata; I observe that you can sometimes avoid abandoning Fock reps (or rather lowest-energy reps) by allowing for gauge anomalies, without giving up unitarity. This is an observation rather than a suggestion; if you look at chapter 2 of GSW, you’ll find it clearly stated that also the subcritical free string can be quantized with a ghost-free spectrum.

Of course, the free string is just a toy model – 2D gravity coupled to scalar fields. To apply analogous ideas to 4D gravity, I discovered the relevant diff anomalies in 4D (multi-dimensional Virasoro algebra), figured out how to build representations of this algebra, and found a formulation of physics to which these representations apply. The main physics lesson is that you must take the quantum nature of the observer into account – QFT is recovered in the limit that the observer is heavy and thus classical.

Lee, you suggest that we should try with new alternative approaches to string theory that have better chances to lead to testable predictions. I would like to see your (as well as that of others) opinion on such an proposal in http://xxx.lanl.gov/abs/0705.3542

First, strings are not postulated, but DERIVED from the (alternative) Bohmian formulation of quantum mechanics.

Second, the theory leads to certain low-energy predictions on particles that can be used to indirectly test string theory as well.