The Trouble With Physics

I’ve just finished reading Lee Smolin’s new book The Trouble With Physics, which should be released and available for sale very soon. It’s a great book, covering some of the same ground as mine, but with significant differences.

This won’t be a usual sort of review, since I’ll mainly concentrate on discussing the parts of Smolin’s book that I found most interesting, and my perspective here is kind of unique, having spent a lot of time writing about many of the same subjects that he covers. I will offer some capsule consumer advice: if you have any interest at all in what is going on these days in fundamental physics, you should buy and read both books. If you really are on a tight budget, and your main interest is in the relation of mathematics and physics, you should get mine. If your main interest is in quantum gravity or the foundations of quantum mechanics, you should get Smolin’s. His is more appropriate for someone with little background in this area, mine contains some significantly more demanding material which requires some expertise to appreciate.

What most fascinated me about Smolin’s book is the personal story behind it. He was a graduate student at Harvard during the same years that I was an undergraduate there, and describes well that place and time. The standard model had just been formulated a few years earlier, and experimental confirmation was pouring in. Many of the people responsible for the standard model were there at Harvard, and there was more than a bit of justifiable pride and arrogance. Smolin was of a philosophical bent, and initially put off:

The atmosphere was not philosophical; it was harsh and aggressive, dominated by people who were brash, cocky, confident, and in some cases insulting to people who disagreed with them.

He studied the philosophy of science and was very struck by Paul Feyerabend’s Against Method (there are also has some amusing tales of later personal encounters with Feyerabend). Feyerabend’s philosophy of science has been described as “anarchistic”; he sees no one “scientific method”, but science as a very human activity, in which all sorts of different tactics are used to make progress towards better understanding. Smolin recognized that much as he would prefer a more deeply philosophical approach, it was the much more pragmatic tactics of people like Coleman, Glashow and Weinberg, who wouldn’t be caught dead talking about the nature of space and time, or foundational problems of quantum mechanics, that was what was really having success.

Smolin begins his book by explaining what he (and I) see as the most important fact about the past thirty years of theoretical particle physics research. We’re in a historically unprecedented situation, with virtually no progress being made on the fundamental problems of particle physics for a very long time, despite huge efforts. In his description, the field has “hit a wall”; I like to describe it as a victim of its own success. The standard model is just too good. It’s too hard to find an experimental result that disagrees with it, and too hard to come up with theoretical advances that will address some of the things it leaves unexplained. Smolin sees the source of the problem in the field’s insistence on sticking with a way of doing science which worked until 30 years ago, but now has become dysfunctional, with string theory only a symptom of the underlying problem. He writes:

I have mentored several talented young people through crises very similar to my own. But I cannot tell them what I told my younger self – that the dominant style was so dramatically successful that it must be respected and accomodated. Now I have to agree with my younger colleagues that the dominant style is not succeeding.

Elsewhere he writes:

My hypothesis is that what’s wrong with string theory is the fact that it was developed using the elementary-particle-physics style of research, which is ill-suited to the discovery of new theoretical frameworks… This competitive, fashion-driven style worked when it was fueled by experimental discoveries but failed when there was nothing driving fashion but the views and tastes of a few prominent individuals.

Smolin was a student of Stanley Deser’s, and during his graduate student years supergravity was a field that was just taking off. He describes getting to know Peter van Nieuwenhuizen and Martin Rocek and being offered a chance to get into the field at the ground floor, one he passed up because he couldn’t believe that the kind of lengthy algebraic calculations they were doing could give real insight:

It was like being offered one of the first jobs at Microsoft or Google. Rocek, van Niewuwenhuizen, and many of those I met through them have made brilliant careers out of supersymmetry and supergravity. I’m sure that from their point of view, I acted like a fool and blew a brilliant opportunity.

Smolin didn’t join the Stony Brook supergravity group, but found that he could make a place for himself in the physics community working on quantum gravity, but using particle physicist’s methods:

… an easy opportunity opened up while I was a graduate student, which was to attack the problem of quantum gravity using recent methods developed to study the standard model. So I dould pretend to be a normal-science kind of physicist and train as a particle physicist. I then took what I learned and applied it to quantum gravity.

Smolin ended up with a post-doc at the new ITP in Santa Barbara, which luckily was running a program on quantum gravity that year. His career tactic almost didn’t pay off:

One day, as we were waiting for the results of our applications, a friend came by to tell me that I was unlikely to get any jobs, because it was impossible to compare me with other people. If I wanted a career, I had to stop working on my own ideas and work on what other people were doing, because only then could they rank me against my peers.

The most powerful parts of the book are the chapters entitled How Do You Fight Sociology?, and How Science Really Works. They give a detailed and clear diagnosis of the problematic way string theory research is being conducted, and decisions are being made about who deserves a job. Smolin has an insider’s point of view, particularly because he himself worked on string theory:

… during the years I worked on string theory, I cared very much what the leaders of the community thought of my work. Just like an adolescent, I wanted to be accepted by those who were the most influential in my little circle. If I didn’t actually take their advice and devote my life to the theory, it’s only because I have a stubborn streak that usually wins out in these situations. For me, this is not an issue of “us” versus “them,” or a struggle between two communities for dominance. These are very personal problems which I have been contending with internally for as long as I have been a scientist.

So I sympathize strongly with the plight of string theorists, who want both to be good scientists and to have the approval of the powerful people in their field. I understand the difficulty of thinking clearly and independently when acceptance in your community requires belief in a complicated set of ideas that you don’t know how to prove yourself. This is a trap it took me years to think my way out of.

Smolin gives many examples of the “groupthink” behavior of the string theory community, while characterizing string theorists as “almost all more open-minded and self-critical and less dogmatic than they are en masse.” He describes string theorists as:

… supremely confident both of the truth of string theory and of their superiority over those unable or unwilling to do it. To many string theorists, especially the young ones with no memory of physics before their time, it is incomprehensible that a talented physicist, given the chance, would choose to be anything but a string theorist.

…Anyone who hangs out with string theorists encounters this kind of supreme confidence regularly. No matter what the problem under discussion, the one option that never comes up (unless introduced by an outsider) is that the theory might simply be wrong. If the discussion veers to the fact that string theory predicts a landscape and hence makes no predictions, some string theorists will rhapsodize about changing the definition of science.

Some string theorists prefer to believe that string theory is too arcane to be understood by human beings, rather than consider the possibility that it might just be wrong.

Smolin finds in the string theory community a sense of entitlement and disdain for anyone who works on alternatives to the theory, with major string theory conferences never inviting people who work on alternatives to speak. An editor from Cambridge University Press told him that one string theorist said he would never consider publishing with the press because it had put out a book on LQG (I see why their publishing my book was out of the question…). At string theory conferences Smolin would be asked “what are you doing here?” or told “It’s so nice to see you here! We’ve been worried about you.” Some friends explained to him that if he wanted to be considered part of the string theory community he had to work not just on string theory, but on the particular string theory problems that were fashionable at the moment.

One problem for physicists trying to get tenured positions that Smolin mentions is that most universities now require letters from 10-15 people evaluating their work, with a small number of negative evaluations sufficient to sink their chances. If you’re working on something other than a mainstream topic, finding 10-15 people who can comment knowledgeably on your work can be impossible. He describes string theorists as mostly submitting the same two or three research proposals. This narrow concentration on a small number of problems is defended by some senior theorists as a “disciplined” approach, one that will more surely lead to progress than encouraging people to pursue a variety of different research directions.

Very recently, Smolin sees things changing:

Until last year I had hardly ever encountered an expression of doubt from a string theorist. Now I sometimes hear from young people that there is a “crisis” in string theory. “We have lost our leaders,” some of them will say. “Before this, it was always clear what the hot direction was, what people should be working on. Now there’s no real guidance,” or (to each other, nervously) “Is it true that Witten is no longer doing string theory?”

One can quantify this new situation by noting that there have been virtually no heavily cited new papers during the past few years, except perhaps for the KKLT one that is part of the landscape story.

Smolin notes that many string theorists (including himself) have often been ill-informed about the exact state of knowledge concerning crucial conjectures about string theory. One example he discusses in detail is that of the finiteness of multi-loop string amplitudes. The state of the subject is that one knows how to precisely formulate them and can show lack of divergences only up to two loops (this is due to the work of d’Hoker and Phong). At higher genus d’Hoker and Phong have a conjectural definition, but have not yet been able to show that divergences cancel. Few string theorists seem to be aware of this, and some of them react with great hostility and shower with insults anyone who mentions this issue (as I’ve done here on this blog).

There’s much else of interest in Smolin’s book, including a lot of material about what he sees as promising ideas in quantum gravity, discussion of research on the foundations of quantum mechanics, and a chapter on “seers”, people doing original work on foundations. These include ‘t Hooft, Penrose, and many others less well-known.

While I agree with just about all of what Smolin has to say about string theory, my own background is different and I see promise in very different lines of research than he does. I’m much more skeptical than him about our ability to get useful experimental data on quantum gravity, and see questions about quantum mechanics rather differently. My prejudice is that, lacking experimental guidance, the thing to do is to try and better understand the mathematical structures underlying the standard model. In the past, better physical models have gone hand in hand with deeper mathematics, and I’ll bet this will continue to be true in the future. Quantum mechanics has deep connections to representation theory, a part of mathematics that unifies many different subfields. It seems likely to me that a better understanding of quantum mechanics will come from better understanding representation theory and its connections to physics.

There’s a lot of other sorts of material in the book that I haven’t discussed, and I strongly recommend that people read the whole thing. It’s very, very good, and anyone interested enough to follow this blog will find it highly rewarding.

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92 Responses to The Trouble With Physics

  1. Gina says:

    Thanks for considering my suggestion and the comments, Peter
    (and thanks nigel and a for the 2 items.)

    Certainly my suggestion was not meant to replace reading your book or Smolin’s but it could be helpful for me to understand what is the essentials, e.g. while reading these books or the elegant books on the other side.

    Your review on Smolin’s book (which is of the same size as what I would like to read) is very personal/philosophical almost like a gathering of two veterans on the same side of a battle but not so useful to understand the essentials.

    Is the critique of string theory is similar to the critique on biologist for not understanding/finding cure for cancer? or is it stronger.
    Is the idea that string rather than point particle can, in principle,
    lead to a “grand theory” a-priori senseless, or just not yet successful, or reasonable-to-start-with but by now clearly a failure?
    10^500 looks fishy but is 10^500 possibilities really that bad?

    I think the main reason for me to be suspicious with “string bashing” is that it did not lead (yet) to interesting science: namely
    to scientific papers (not popular reviews and books). Why is that?

  2. Lubos Motl says:

    Dear Peter,

    you completely missed my point. My point was not to attack other people than you. It was, on the contrary, meant to prove that you are the #1 moron on this crackpots’ discussion forum. ;-)

    Best
    Lubos

  3. Peter Woit says:

    Gina,

    Again, for the short version, I recommend reading my 2001 article. Yes, 10^500 possibilities really is that bad. All indications are that it makes it completely impossible to ever extract a real prediction from the theory, which is deadly.

    The situation of string theory is very different than that of cancer research, an analog would be if current cancer treatments not only didn’t help at all with the disease, but made it much worse.

    “string-bashing” by itself doesn’t lead to interesting new science, except in the sense that encouraging people to stop working on a failed idea and look for something else to do may have a positive effect. Lee is one of the leaders of a very active research program that is working on new and different ideas, and he has published a long list of scientific articles on this. I have my own ideas about alternatives to string theory, have written much less about this. For some of what I have written see my long 2002 paper on the arXiv.

  4. Peter Woit says:

    Lubos,

    Actually I did get that that was the point of your comment. But, sorry, if you want to write comments here about what a moron I am, you have to avoid at the same time attacking other people as morons, since I’m not going to allow that.

  5. Tom Killick says:

    I am not a physicist. I am an engineer. It has always seemed to me that postulating un-testable hypotheses is more the domain of religion or philosophy than of Physics. I would like to draw you attention to work being done by Charles Francis that is evolutionary, exciting and that does belong in the realm of Physics. This work claims to have bearing on dark matter, the age of the universe and more. It is also eminently testable and appears to explain currently anomalous data and makes specific predictions about future data.
    I am intrigued by work being done by Charles Francis for much the same reason as you concentrate in your review of Smolin’s book on the areas that most interest you, the personal story. I went to high school (in fact a very prestigious private catholic boarding school) with Charles Francis the late sixties and early seventies. I can unequivocally say that he was the most brilliant mathematician and logical thinker I have ever met. At sixteen he could produce elegant, concise and original proofs that allowed me, other classmates and his teachers to begin to understand the power and beauty of mathematical physics. I know he went on to Cambridge and Birkbeck college in London to finish a number of degrees. He is a very eccentric individual which has allowed him to focus on solving what he calls “the really important problems” for the last 40 years. His eccentricity has also isolated him from much of what I assume to be the hubris of modern physics.
    His paper which in his characteristically un-self effacing way is titled

    “Does a Teleconnection between Quantum States account for Missing Mass, Galaxy Ageing, Lensing Anomalies, Supernova Redshift, MOND, and Pioneer Blueshift?”

  6. Gina says:

    Here is my a priori take on this before reading any of these books.
    _______________________________________________

    1. The question of quantum gravity and this grand unification is a
    major intellectual/scientific challenge.

    2. String theory offers understanding for this problem as well as deep and interesting insights on various issues from physics. Motl list of 12 appears to be very impressive. (And apropos Motl, I even conjecture, perhaps contrary to this example, that most string theorists are neither bullies nor male Chauvinist.) Not many other scientific theories can match such a list. String theory is the only major theory that offers such understanding for the unification problem. It also led to great mathematics.

    (Well, there is some amount of over-sale, and discussions with serious faces of all this multiple universes stuff but this is not that unusual.)

    3. There are serious problems with string theory concerning the possibility to draw concrete predictions that can be verified. There are also many possible string theories. (I do not share the interpretation that these limitations of the theory are fatal. And maybe we cannot hope for more.)

    4. String theory is still rather tentative. It is quite possible that the
    theory will fade away because of its difficulties and it is also possible that it will be replaced by a different theory which does a better job. It is possible it will prevail.

    ___________________________________

    As for the discussion, I cannot see, nigel, how string theory can be “dangerous” and I cannot see, Peter, how things can between 2001 and 2006 have gotten “much much worse” (but I can see you being much much more excited.) And “dying (like Maxwell) with a firm belief in a flawed theory”, nigel, can serve as a nerd’s curse
    but it is not significantly more terrible than just dying. (Unless the death is caused by the theory.)

  7. Lubos Motl says:

    Virtually all of string theorists are nice people who never argue with anyone else, they’re not chauvinists, and most of them are feminists. Most of them also think that string/M-theory are robust twin towers that are not threatened by any social effect or passionate proponents of alternative theories or proponents of no theories, and they almost always try to avoid interactions that could lead to tension which also gives them more time for serious work. Almost no string theorists drive SUV and they produce a minimum amount of carbon dioxide.

  8. Peter Woit says:

    Gina,

    Discovering that your theory has 10^500 times more solutions to it than you thought it did really does count as “much worse”. Virtually every string theorist will admit that the “landscape” is a huge problem for the theory. Things really are much worse now than they were 5 years ago.

  9. anonymous says:

    Hi,

    I came across this weblog after Amazon automatically recommended me Peter Woit’s new book. I went through it and I was amazed to see the extend that some disagreements can take and the way that people, affiliated with high profile institutions, behave when they should be models for the rest of the community and their students. Congratulations!

    Personally, I find the situation rather interesting and I really hope something good will come out of this, whether it is in favour of string theory or not. I would like to make a comment, however, on the situation the way I see it. Please keep in mind that I am not a string theorist and I wouldn’t even call myself a physicist in general. Nevertheless, here it is.

    Let’s see how long it takes for someone to get a PhD. Usually it is 4 years as an undergraduate and 5 years as a postgraduate. Most of the young people interested in string theory feel that they should start studying the subject while undergraduates. I guess that is why MIT introduces string theory classes and Zwiebach publishes books on “undergraduate” string theory. It has to do with demand, the customers have to be satisfied somehow. Blame it to the hype. In the graduate school you are forced to publish something, as if the rest of the thousands of people that form the “community”, or physics as a science in general, is going to be saved by the students’ publications. I may be wrong on this and it might be indeed necessary to publish as many papers as possible although I really doubt it. So, what is left? Narrow minded people, they have been doing strings or whatever all their life so you can’t expect anything better, or disgusted and bored people who realize that life can be exciting without physics and go work for the industry, capitalizing their PhDs by getting nice flats and nice cars and going in nice places for their vacations.

    I recall an undergraduate telling me that he wants to get his degree as soon as possible and go do a PhD in string theory without doing a masters first and that is why he chose to study for a 3 years bachelors ( this senario is possible in some countries ). I mean, how is that possible? Senior people are very well educated, no doubt about that, but what about the undergraduate/graduate folks? I am looking at the well known QFT book by Peskin and Schroeder sitting in my bookself right now. How long does it take for someone to read it, solve the excercises and be able to reproduce the results mentioned in it? In other words, master it? What about general relativity? Cosmology? Non relativistic quantum mechanics? Particle physics ( with a phenomenological bend )? Statistical physics? Catch up with the rest of the community? Interact with people working in other fields like for example condensed matter or mathematics. Two or three years? If not, then how does someone attempt to solve a problem when he doesn’t even know what the problem is in the first place? How is critical thinking going to be developed the way the educational system works?

  10. Ted Fails says:

    Im an amateur at this, but it seems to me that if there is already a
    huge uproar over explaining the number “one” as arising naturally
    in physics (ie, the CC), then how is it that anyone is comfortable with a finite number like 10^500? If this number is not infinite then
    isnt it really wierd? (If it IS cardinal C, then why is it refered to as
    10^500, which, by the way, is a very long way from C.)

    In a unital algebra, “one” will frequently be present, but I find 10^500 a much more curious number.

    Anyone please comment.

  11. ak says:

    tg claimed:

    ‘So I summarize that string theory is an with high degree of mathematical consistency but which clearly needs experimentation. Its difficult math and difficult physics, so therefore time is necessary to come to an appropriate conclusion.’

    I point out that the bare fact that string theory centers a discussion of dominating sociological and/or ‘philosophical’ character which in fact can be led largely decoupled from scientific arguments ‘disproves’ the above sentences. In fact there seems to be nearly a consent, even across the frontiers, about a certain lack of ‘predictions’ implied by string theory, while the disagreement centers mainly about the degree of this absence (which puts a claimed-to-be ‘theory of everything’ in a rather ironic light) and/or the ‘interpretation’ of this generally undenied fact (‘it takes time’). I think that philosophy is fine as long as it supports or manifests the ‘explaining’ aspects of a mathematical formalism which shares as its necessary property ‘prediction’, I remember to have learned this years ago being still an undergraduate from a popular book by David Deutsch, his point was more or less that in purely logical terms a theory wouldn’t need to be able to explain phenomena AS LONG as it makes the right (i.e. verifiable) predictions about them. To summarize the above discussion one can only conclude that string theory goes the opposite way, it more or less seems to suggest that prediction is fine but nothing compared to the intriguing implications suggested by the theory’s ‘explanation’, this culminates obviously in this ‘landscape’ argument, where prediction is intrinsically senseless and explanation (the anthroposophic principle, the multiuniverse) puts itself into the perspective of initiating a ‘new era’ beyond Kopernikus, Einstein et al. I mention that one could parallelize these observations with not-quite recent arguments of german philosophers/sociologists (!) Adorno and Horkheimer whose ‘Kritische Theorie’ predicted and observed exactly the above discussed failure and tendency of modern rationalism and science in general to become ‘mythological regression’, even not as a corollary of the scientific method but as an intrinsic principle hidden in rational progress, danish philosopher Kierkegaard already observed in the 19th century that ‘this century has produced more myths than any era before’, I wonder what his comment would be today.
    I could add that concerning my personal experience with ‘modern physics’ and mathematics I already doubted the mathematical rigor and consistency of ‘the standard model’ which was the point where I changed to mathematics, from the constant efforts of mathematicians to understand recent and non-recent concepts in ‘modern physics’ (only to mention the ‘path integral’, mirror symmetry) I can only doubt the above mentioned term of the claimed ‘mathematical consistency’ of string theory, even the meaning of this word combination is unclear (what does it mean: a theory which is logically consistent, should this be a particularly ‘nice’ feature of string theory or is ist just the most necessary condition for a mathematically formulated physical theory to become science?) and as it seems it is relatively hard to ‘believe’ that it is physics at all, it might be difficult and ‘in some sense’ consistent, but possibly neither mathematically consistent nor difficult as a physically theory, so maybe one could say it is an extremely difficult and sociologically ‘consistent’ metaphysical theory ?
    (I apologize if this became a bit polemic.)

  12. Lee Smolin says:

    Dear Peter,

    Thanks for the very thoughtful review. I have been distracted by some great personal blessing but see tonight that my book is available on Amazon.com and that Lubos has posted a two star review as you predicted. I am not interested in playing a game with Lubos or anyone else whose modus operandi is ad hominum attacks rather than serious engagement about ideas. (His attribution of some positive comments about my book made by Sabine Hossenfelder to the intellectual inferiority of women is for me so far beyond the pale, I really have no energy to further engage with him.)

    I wrote a book which treats those with whom it disagrees with a great deal of respect and admiration. The point is not who is a member of what community or who is esteemed by whom, it is about which ideas are right about nature and which are wrong. I wrote about string theory, not to demean it, but because it was the best idea we had about unification and if it is in crisis then we have reason to reexamine our presuppositions which led us to believe in it so strongly (and I do mean us.) My book arose out of such a re-examination and its value, for me, is that it contains proposals for what are the wrong ideas that took such a promising idea to its present crisis. So I am not willing to engage with people who are not willing to recognize good faith and respond in kind. But I am of course happy to discuss with those who takes the time to read it and responds in the spirit in which it was written.

    Thanks,

    Lee

  13. Who says:

    Congratulations on the aforementioned blessing. Hope all are well:
    though I and others know you only through your work, many must be wishing you joy.

  14. Gina says:

    Rather than attacking string theory directly a more promising way for trying to see what is wrong (if anything) with it to try to question the basics of extremely successful theories which preceded it. Peter, Lee is there some “QED bashing” in your books? (Even “QCD bashing” is already considered bad sportsmanship.)

  15. 10^500 says:

    Oversimplified answer to Ted Fails: “how 10^500 comes out?”

    Strings want 6 or 7 extra dimensions, and to predict anything at low energy you must know their geography. Some complicated geography (holes and branes here and there) seems needed to try getting the complicated physics we observe. Strings tell that all of geography is dynamically fixed by vacuum expectation values of fields. There are many fields: a few fields describe the size and shape of extra dimensions, others tell the amount of each magnetic-like fluxes that can wind around each hole, etc, etc, etc. With a normal potential, each field has a few possible minima, and thousand of fields can have few^thousand minima.

    10^500 is so many that, whatever we measure, string theory might have 10^100 solutions that practically look like it, altough finding them might be practically impossible.

    Despite all impressive achivements, and despite Lubos Motl, this seems the end of the story.

  16. Gina says:

    It was a pleasant surprise that I could read Peter’s 2001 paper
    feeling that I understood most points Peter had made. This paper is almost disjoint (or orthogonal) to what I asked Peter. (Maybe 2-3 specific “anti string theory” claims can be extracted.) Part of the paper is a sort of philosophy of science look at particle physics and string theory of the last 3 decades geared towards “philosophy of funding of science”. Philosophy of funding of science is an interesting and important subject worthy of discussions and debates but it is a separate issue to the “case against string theory” (as a scientific theory). I would still be happy and greatful to see a summary of the “case” against string theory along the lines I asked.

  17. TheGraduate says:

    To Gina:

    (Well this is by no means authoritative but the anti-string theory case seems to be roughly as follows:)

    1. String theory does not predict anything

    2. There is currently no obvious way to modify it so it would predict something

    3. String theory is reducing the probability that other (possibly more predictive approaches) will be tried.

    All of these points can be expanded into sub-cases but I think they cover all the categories of objections.

  18. Lubos makes me puke! says:

    Gina- I would suggest that you visit the archives of this Blog starting with March of 2004 which has a good article about Peter and his education and qualifications. You can skim the articles and read the important articles about String theory fairly rapidly. This would help you understand that this is a very complicated problem that has arisen from virtually a idea that never had any of the empirical physical evidences that is required for the scientific method. The beauty and complexity of the mathematical calculations necessary to explore the extra dimensions of string theory lured a lot of our most brilliant and gifted students to work for many years only to find that they had invested their time unwisely. Rather than admit their mistake, some like Motl will do anything to keep this dogma a science. Something it has not been for a long time. We all owe our gratitude to Peter for making us aware of this problem.

  19. ak says:

    I have to admit that I still tend to get headache reading papers about particle physics whatever their background and philosophy might be, at least from my point of view they mostly tend to involve a considerable amount of mathematical sophistification but themselves completely lack the beauty and conisistency of the mathematical results and theories involved, in contrary they tend to mix up rigorous mathematical results with speculative ideas and concepts from mathematical and/or physical ‘folklore’, which makes ist extremely difficult for ‘non-insiders’ to decide what is still logically consistent deduction and what is wishful thinking or black-box deduction. I assume, and Peter seems to indicate that, that the ‘problems’ modern physics faced in the development since the 1970s derive as much from its desynchronization with mathematical justification of the concepts involved as with with its disconnectedness from experimental evidence. Motls list seems to reflect either intrinsic features of the theory which seem to be nearly tautological (‘unity of supergravities’) or concepts which are as interesting as yet poorly understood from a mathematical viewpoint (AdS/CFT/ mirror symmetry). From this point of view Peters attempt to re-view the mathematical concepts of the standard model seems to be promising; one could finally hint to an article of Berhelm Booss-Bavnbek, who judges post-war mathematics to be ‘deformed’ in a characteristic manner by aims of ‘fictional warfare’, this point of view is possibly not completely irrelevant to the discussion here (unfortunately in german):

    ‘Symptome der militärischen Deformation: undurchdringliche Komplexität, rücksichtslose Kreativität und täuschende Vertrautheit’

    http://www.uni-muenster.de/PeaCon/wuf/wf-90/9021101m.htm

  20. Pingback: Assistant Professor Lubos Motl’s disgraceful attack on Lee Smolin « Gravity

  21. Gina says:

    Motl:

    Can you please tell me (just a few sentences understandable to a laywoman) what is your opinion on the two claims:

    1) That string theory cannot predict anything and will not be able to.

    2) That there are over 10^500 possibilities which makes things worse.

    many thanks in advance –Gina

  22. Who says:

    “The Trouble with Physics” (topic of thread) continues to be #1 on the Amazon general physics bestseller list
    http://www.amazon.com/gp/bestsellers/books/14560/ref=pd_ts_b_nav/102-4540543-7840144

    at least it was 9AM to 4PM pacific time today, could of course be different at 5 PM—list changes hourly.

  23. Ming says:

    “My prejudice is that, lacking experimental guidance, the thing to do is to try and better understand the mathematical structures underlying the standard model.”

    I disagree with you 100%. The farce of string theory has shown definitively that more mathematics isn’t the way forward for physics. I think the way forward is that we need to re-examine the basic foundation of the whole edifice of theoretical physics and look for the missing key pieces (of physical concepts, not mathematics) that everybody has so far overlooked. We need to question the foundation of everything and take nothing for granted. Looking for the easy half-hearted way out by using ever fancier mathematics simply won’t work.

    Unfortunately this kind of work is despised by most practising theoretical physicists, who’re almost all of the “problem solver” variety. What we need desperately are more “seers” as Smolin described them, or “thinkers” may be a better word for it because it doesn’t have the superstitious connotations of seers. If we look back at the history of theoretical physics, the most prominent advances were almost always made by thinkers and not problem solvers. Einstein being the best example of a great thinker (though he’s also a darn good problem solver). Thinkers can think outside of the box (i.e. the existing formalism of theoretical physics), while problem solvers can only work within the box. The almost complete stagnation of theoretical physics for the past half century is due to an almost complete lack of quality thinkers, with all physics jobs going to the best problem solvers. As long as this extreme imbalance between thinkers and problem solvers persists in theoretical physics, I’m afraid there’s no hope for true advances… IMHO

  24. Ming says:

    I just noticed that a recent 5-star review of Smolin’s book has been deleted while Lubos’ 2-star review is getting suspiciously high number of “helpful” votes. It looks like someone is actively (and desperately) “reporting” positive reviews of Smolin’s book while artificially generating helpful votes for Lubos’ review. I’ve only seen this kind of behavior from the site of another “science” book, the author of which is a total crackpot, and he is writing fake 5-star reviews for his own book while trying to report and delete all negative reviews (sad thing is he succeeded). Didn’t know that string theorists/supporters can also fall so low…

  25. Ming,

    I agree with you 100%. The usual paradigm:

    Standard model and general relativity are great. The only thing left is to put them together.

    lead us in a corner. The only way out of this corner is backward. No amout of clever problem-solving will help.

  26. ak says:

    I remark that it could be already ‘mythological regression’ to assume a GUT would actually exist. Periods of extreme idealism were quite frequent not only in science but also in philosophy or art (Hegel, Kant, Nietzsche) and Lubos gives an example of even biologists thinking of ‘their’ path to the universally saving GUT. The crisis of modern physics is not their lack of progress towards idealism, it is its implicit contact with the natural limitations of human (experimental) insight into nature itself (only to mention the energy scale of reasonably realizable accelerators). Possibly the non-existence of ‘seers’ derives from the fact that there ‘is nothing to be seen’ which would not go beyond the intrinsic limitations of human insight, at least derived from the standards of current technical ability. Apart from the fact that Einstein ‘knew’ what would have to be predicted, there in fact was experimental data (Michelson-Morley) giving at least subtle traces of the directions to choose, are there any comparable ‘traces’ today (Neutrino mass, dark matter?), one could doubt this. Apart from this, from a non-mathematical point of view idealism and regression were always closely connected, I only mention german idealism and its consequences for the history of the last century, it could be a characterizing property of a ‘theory of everything’ that it predicts in fact NOTHING, so string theory follows the ‘dialectic principle’ of human rationalism maybe in its purest form. I am personally quite happy about the existence of small-scale problem solving which, as a matter of exactness of the techniques involved, has from my point of view at least the potential to be of ‘practical use’ in human scale, that is, in human ‘everyday life’. I objected a tendency in theoretical physics to substitute the reality of existence as human beings and the diversity of (even physical) reality by concepts of extreme idealizing, at the same time simplifying, potential. The current status of absence of ‘predictiveness’ of string theory is possibly just a corollary of the wish to include apparently uinversal ‘explanation’, under whose regime details as ‘mathematics’, ‘logic’, ‘rationalism’, ‘predictiveness’, in the end maybe ‘science’ itself seem to lose their relevance or status as guiding (and limiting) principles they acquired over the thousands of years of growth of human knowledge (at least in the ‘exact sciences’). Possibly it is the moment where the exact sciences lose their insight into their own limitations where they end to exist as ‘exact sciences’ and turn themselves into mythology, I already said this above. For my own part, I am quite happy to consider exact sciences as ‘exact’ but limited and the other disciplines of human thinking (which EXIST, even to me as a mathematician) as ‘inexact’ but potentially unlimited, possibly the status of modern physics gives a hint towards the growing disassociation of the scientific worlds or human thinking in general, which would in the end lead again towards the concept of ‘thinker’: maybe it would be Einstein, knowing the history of post-war physics and societies in general, to conclude that there is a certain whisdom in preserving ‘mythology’ as ‘mythical’ and ‘exact sciences’ as ‘exact’, maybe this is what would have to be ‘seen’ from his perspective.

  27. Lee Smolin says:

    Ming,

    I’m not doing anything, it is very sad to watch. I wrote two books before, there was a lot of disagreement, for example from string theory friends who told me that my idea of the landscape of theories was silly and there would soon be a principle of vacuum selection that gave unique predictions. But no one behaved badly. What is really sad is that there are many string theorists who are ethical and act and talk in good faith, if I were them I would be appalled to let me field be so represented. Besides which this kind of behavior provides strong evidence for the claim that there is something pathalogical in the sociology of the field.

    Thanks,

    Lee

  28. ks says:

    Just for the record. String theory has nothing to do with the philosophy of “german idealism”. Attributing the believe in hypothetical stringy objects that are not detectable but shall be present for complicated theoretical reasons to Kants critics of pure reason or his categories of mind a priori or Hegels self-reflection of absolute mind and its projections into history, is hilarious. I do not even want to imagine what Nietzsche had made out of this drive into self delusion and science-as-cult beyond its empirist tradition. Maybe an appraisal of John Horgans writings as being sound? German idealism is close to the contemporary radical constructivist/deconstructivist philosophy, to existentialism, phenomenology etc. not to a naive believe in the objective existence of ones own intellectual phantasies.

  29. anonym. says:

    ” Didn’t know that string theorists/supporters can also fall so low… ” – Ming

    They are unable to respond any other way, they have no other responses to give.

  30. MoveOnOrStayBehind says:

    “German idealism is close to the contemporary radical constructivist/deconstructivist philosophy, to existentialism, phenomenology etc. not to a naive believe in the objective existence of ones own intellectual phantasies.”

    Here is a good example to what conclusions german philosophers are lead to, in this case concering the Higgs mechanism:
    http://www.dpg-tagungen.de/archive/2006/dortmund/akphil2.pdf
    Unfortunatly this is in german. What is being said there is that “neither an ontological, nor an epistemological interpretation of the Higgs mechanism is tenable”; this follows fram a “critical analysis”.

    The link given above, “Symptome der militärischen Deformation: undurchdringliche Komplexität, rücksichtslose Kreativität und täuschende Vertrautheit’” in another beautiful example of political ideology mixed up with science.

    Good that there are other parts of the world where science is moving on, although I am getting concerned about the US too, after reading the opinions in this blog here.

  31. ak says:

    no, there seem to be some ‘misreceptions’, I did not compare string theory to ‘german idealism’, the argument was that to believe in the existence of a GUT could be a form of idealism, there is no such thing as pure ‘naive believe in the objective existence of ones own intellectual phantasies’, string theory takes place on a sociological/philosophical background and I just point out that it was Einstein co-initiating the belief in the existence of a GUT. My point was that real progression in modern physics could mean to be a little bit closer to Kierkegaards criticism of Hegel (opposing his dominant position, claim of unifying logical concepts etc.) and from what I understood, Peter and Lee move a bit in this direction. By the way I don’t think that ‘german idealism’, as a philosophical phenomenon, is very close to existentialism or deconstructivism and ‘to move on or to stay behind’ is exactly what this discussion is about.

  32. ak says:

    I have to correct myself in the sense that the point is that to rethink modern physics with the explicit aim of a GUT remains pure ‘idealism’ as long as there are no fundamental experimental guidelines to show what exactly a new theory should predict or explain BEYOND the capabilities of the existing models. The unexplained constantness of the speed of light in a vacuum was Einsteins starting point, maybe I am not quite informed, but I do not see that there are any compareable fundamental facts pointing beyond the existing models today. In this situation the string theorists can hardly blame non-string-theorists to develope alternative pictures, one could for instance raise the question why not anyone seems to be interested in the notion of ‘symplectic spinor’ or symplectic Dirac operator, from a physical point of view the symplectic Dirac equation could possibly be the starting point for a geometric theory of bosons (since it involves the ‘symplectic Clifford algebra’), a not quite new paper

    http://www.mathematik.hu-berlin.de/~klein/ftr.ps

    shows that there is a natural notion of pseudo-differential quantisation involved over sections of a certain line subbundle of the sympletic spinor bundle, on the other hand the metaplectic representation implies the Schrödinger equation for linear hamiltonian systems on R^{2n} and is reflected in some sort of Lie derivative

    http://www.mathematik.hu-berlin.de/~klein/liabl.ps

    the picture is admittedly not quite coherent, but as a physicist, i could possibly just ‘couple’, for instance over Kaehler or Calabi-Yau manifolds, the Dirac operator over the ordinary spinor bundle with the symplectic Dirac operatior over the sympl. spinor bundle (taking tensor products and operator ‘sums)’ and see what ‘happens’, for Calabi Yau manifolds a natural notion of Maslov index would be involved and would give rise to some notion of ‘quantisable’ Lagrangian foliations, which would correspond to the dimension of the kernel of the square of some restriction of the symplectic part of the coupled operator etc etc, maybe a new ‘TOE’, who knows.

  33. ks says:

    I just point out that it was Einstein co-initiating the belief in the existence of a GUT.

    Actually this goal must be attributed to Newton and all his followers. Einstein and other quantum theorists of the first generation destroyed the old worldview and broke it into two incompatible parts without losing the researchers inherent destination of a complete and consistent physical explanation of the whole world. There is no point to make in the inexistence of a GUT because its existence is undecidable unless it exists. It can’t be disproved by reason. We can only get stuck. Hence demystification doesn’t help us because there is no other side of true reason but just a decision to make for everyone when its time to give up, which is finally subjective.

    What really happened with the desire of a GUT is that it became an aspect of mass/pop-culture and its proponents rock-stars of popular science magazines ( “Einsteins legacy” etc. ) and books. Physicists and to a lesser degree mathematicians are our last heros the last people who truly “transgress the boundaries” which is properly mythological and part of the fascination. Besides the person Stephen Hawking it was ST that had been in the focus of the economy of attention of fundamental science in the last decades. String theory is both a highly esoteric and speculative branch of mathematical physics and the pop culture of the TOE. This tension makes it interesting even for visitors who are by no means “active researchers” in the sense of Distler. I’m not claiming that depressing the public about the TOE wouldn’t be healthy for the theoretical physics community even if it’s going to shrink to the size it had at Einsteins time.

    I have to correct myself in the sense that the point is that to rethink modern physics with the explicit aim of a GUT remains pure ‘idealism’ as long as there are no fundamental experimental guidelines to show what exactly a new theory should predict or explain BEYOND the capabilities of the existing models.

    This is undisputable. Reason without experience is empty, experience without reason is blind, as Kant said.

  34. D R Lunsford says:

    ks said

    What really happened with the desire of a GUT is that it became an aspect of mass/pop-culture and its proponents rock-stars of popular science magazines ( “Einsteins legacy” etc. ) and books. Physicists and to a lesser degree mathematicians are our last heros the last people who truly “transgress the boundaries” which is properly mythological and part of the fascination.

    Well I don’t really agree. The desire for unity is completely justified, as is seeking it in geometry. All three major developments since Newton – Maxwell, Einstein, and Dirac – are based on geometry and the idea of unity, or rather as Finkelstein would say, “relativization”, which amounts to simplification of the underlying Lie algebra of observables by decontraction. The problem seems to be that the current practitioners are just uncommonly bad at finding the key physical ideas, because they are too enmeshed in arcane mathematics. Klein, Courant, Weyl, all warned us this would happen.

    -drl

  35. ak says:

    I am afraid not to understand the dialectic principle of these two points:

    ‘The desire for unity is completely justified, as is seeking it in geometry.’

    ‘The problem seems to be that the current practitioners are just uncommonly bad at finding the key physical ideas, because they are too enmeshed in arcane mathematics.’

    The ‘desire for unity’ is claimed to be derivable from purely mathematical reasoning, at the same time to be ‘enmeshed in arcane mathematics’ is attributed to the unability of finding ‘the key physical ideas’. This could hint to some key misunderstanding of string theorists reasoning, taking on one hand mathematics as a guideline for fundamental aims and on the other hand attributing subsequent experimental deficits of the theory to the unability of ‘practitioners’ to find the key physical ideas while being absorbed in mathematical reasoning. To resolve this one should possibly follow the contrary strategy: to take experimental facts as the origin of thinking (not taking experiments as the corollary of mathematical idealism) and to use on the other hand plain mathematics as the tool to derive a theory from this experimental starting point (I point out that my above statement about a possible ‘TOE’ derived from symplectic spinors was of substantial ironic character).

  36. D R Lunsford says:

    ak said

    The ‘desire for unity’ is claimed to be derivable from purely mathematical reasoning, at the same time to be ‘enmeshed in arcane mathematics’ is attributed to the unability of finding ‘the key physical ideas’.

    No one ever claimed it was derivable from “purely mathematical reasoning”. Indeed the intuitionists firmly believe that such a thing does not exist, and that both math and physics are stimulated by mutual interaction. Finding the right physical idea is an irreducible activity – finding its mathematical realization is not. By “arcane” I mean – disconnected from “physical reasonableness”. Certainly there are many complex mathematical structures that are eminently reasonable. The main activity of the physicist is to come up with physical ideas that are reasonable and tractable. That is what is completely missing these days.

    -drl

  37. ak says:

    ‘The main activity of the physicist is to come up with physical ideas that are reasonable and tractable. That is what is completely missing these days.’

    I still do not agree on the form of this conclusion. It is a myth Einstein derived Relativity from pure physical intuition, there was an experimental guiding principle which lead to concepts like ‘Lorentz invariance’ and Minkowski space (Michelson-morley). From THIS point, it was in fact a pure ‘thought experiment’ to generalize to curvature, geodesics and so on, but the experiment could in fact qualify the result of these thought experiments to be true. In the current situation of modern physics there seems to be neither a clear physical guiding principle derived from experiment nor a possible way to judge the result of a wide variety of thought experiments, so one cannot in fact blame the state of string theory to the absence of ‘thinkers’ producing reasonable physics. It is exactly this belief in ‘new physics emerging from human brain’ which lies at the esoteric origin of string theory and potentially also of related concepts.

  38. amused says:

    Thanks for this review Peter, I’m looking forward to reading the book
    (and yours).
    Smolin makes some astute observations, but it’s one thing to describe the problem and another thing to find a viable solution. As Smolin points out, young peoples’ job prospects in formal particle theory are determined by how they are viewed by senior influential physicists, and since most of the latter are string theorists (at least at the leading US uni’s) it puts the non-stringers at a huge disadvantage. As far as I can tell from reviews of the book and what he has written elsewhere, Smolin’s solution for this seems to be some kind of “democratisation” where funding and jobs get distributed over various areas in proportion to the number of people working in them. What do you think about this? Personally I’m against it. One reason is that it just replaces preferential weighting for string theorists by preferential weighting for people working on some broader selection of areas. What if my preferred research area is not among these? Or if the representative for my area on the “committee” is not very eloquent (he neglected to develop his salesman skills through hyping of our area to the public) and therefore can’t get us a decent share of the pie? Or if I suddenly find that there is something exciting in a non-represented area that I want to work on? Besides that, I do think these kind of things should be left as much as possible to “market forces”. The problem is that at the moment we don’t have a genuine free market; it’s more like a monopoly a la Microsoft.

    Anyway, if Peter will indulge me I’ld like to propose a different solution: How about just letting people work on whatever they like, without preferential weightings for any particular areas, and evaluating them solely on the basis of the progress they make? This requires of course some objective measure for evaluating “progress”. We need something that can be used to evaluate and compare people across different areas. The normal thing in academia is to base this on journal publications. Problem is that people don’t care much about journals in theoretical hep these days. When you write a paper you stick in on the archives, where it gets seen by the senior influential people in your field, and your stock goes up or down depending on what they think of it. Subsequent publication of the paper in a supposedly major journal is usually routine and doesn’t mean much. This situation is ok for evaluating and comparing people within the same area, but how are you supposed to compare people across different areas? Although they publish in the same journals there is no way to tell the relative quality and significance of their works just from “major” journal publications, since it doesn’t take much to get published. Similar things can be said about citation counts (which not only measure the significance of the paper but also the well-connectedness of the author and the size and popularity of the area in which the paper lies).

    However, there remains one physics journal which is still non-trivial to publish in: Physical Review Letters. So how about using number of publications there as the evaluation measure? (The weight of each paper should of course be normalised according to number of co-authors, and with a further appropriate reduction for young people who are just going for a ride on the coattails of seniors.) While it is true that some areas of physics (e.g. condensed matter) are easier for getting published in PRL than formal particle theory, within the latter area there doesn’t seem to be any biases (e.g. it is not unusual for both string theory and LQG papers get published in PRL) so it would seem to be a level playing field for all. The string theorists surely won’t have any objection to this – since they are so brilliant they will surely welcome the opportunity to prove it in an objective setting. In fact I’m sure it’s only their natural modesty which has prevented them from filling up the pages of PRL already. It will also give a chance to the hardcore younger stringers to finally silence those “penis envy”-afflicted cynics out there, who go around disparaging them for being mindless clones, absorbing what they are spoonfed like sponges but incapable of doing anything original and significant on their own.
    (Whoops, seems like I might have slipped into string-bashing mode at the end there ;))

  39. Ron Macnaughton says:

    I’m a high school physics teacher who just yesteray was asked what I thought of String Theory. My student had trouble understanding what he thought was the deepest theory developed so far.

    I explained how most astronomers used to believe planets moved in circles or circles on circles. Eventually Kepler showed only elliptical orbits explained the observed positions of Mars.

    I gave the opinion that String Theory makes some assumptions and it might come close to explaining reality, but I didn’t think it would ultimately be successful, just as epicircles went into the dustbin of science.

    I said that’s only a high school teacher’s opinion, but many brilliant people worked on it and believed it.

    I think the main problem is that String Theory doesn’t seem to include General Relativity.

    I find the sociology of science rather interesting. We talk about heroes who have a pure drive for understanding, but Tycho Brahe gave Kepler the Mars problem, because he thought it would be too hard for the young whipper snapper to solve. Correct theories (plate tectonics) get rejected for decades. Wikipedia still lists only string theory as a theory for quantum gravity, even though many alternatives are out there.

    I read “moron” comments on this blog which I find embarrassing when I hope to inspire young people to take up science as a career.

    I can’t wait for my copy of both books to arrive.

  40. woit says:

    Hi Rob,

    An important thing to explain to students about science is that it makes testable predictions that can be checked. Things like string theory are very speculative ideas that some people someday hope will become legitimate, testable science, but they’re not there yet. Some of us think it never will get there, some are more optimistic.

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