Book Review: Lee Smolin, The Trouble with Physics
The first point is that the book is not an attack on string theory, at least in the strong and uncompromised sense Peter Woit’s Not Even Wrong probably is. (I haven’t read that one, but I’d be surprised if it was half as sympathetic to string theory as Smolin’s is). Smolin makes clear that he does not think that string theory is a failure or that research in it should be abandoned. The provocative title and cover of the book (as Smolin has said) and the promotional material from the publishers (as Bee remarks) are misleading in this respect, being clear attempts to boost sales by fueling controversy. I am not going to speak ill against the nice publishers who gave me a free book, but just say that readers put-off by what seems an aggressive, unconstructive attack should give the book a chance.
(I’m just having an absurdist vision of Woit and Smolin playing a bad cop-good cop routine against a handcuffed string theorist! Probably inspired by this old Cosmic Variance comment, by far the funniest take on the String Wars I have ever seen.)
Smolin opens the book with a provocative question: Given that the past twenty-five years have been the only quarter of a century in the past two hundred years in which fundamental theoretcal physics has not made a significant progress in our understanding of the universe, what are the causes of this situation and what can we do to revert it and bring back the glorious times of the Einsteins, the Heisenbergs, the Feynmans or the Weinbergs? What does physics need to get moving again?
He next describes the five “Great Problems” which need to be solved: finding a theory of quantum gravity; solving the foundational problems of quantum mechanics; finding (if there is) a theory that unifies all the forces and particles found in nature; explaining the values taken by all the parameters of the Standard Model; and explaining dark matter and dark energy. Then comes a fast tour through the history of physics with an emphasis on the idea of unification, that takes us through several chapters from Galileo’s of principle of inertia “unifying motion and rest” to the formulation of the Standard Model which describes all forces as manifestations of gauge symmetries. The explanations of different topics in these chapters are gentle, clear if not too comprehensive, and directed always to the lay reader. The choice of “unification” as a theme has some odd consequences as for example more space in the story is dedicated to the Kaluza-Klein theory than to the discovery of quantum mechanics and quantum field theory (which, one could even argue, provided a fundamental unification not mentioned by Smolin, between discrete particles and continuous field waves). The next chapters build up to the origins of string theory by chronicling the first (failed) attempts to unify forces beyond the Standard Model and to construct theories of quantum gravity. There is an interesting personal memory of the days in the mid ‘70s in which supergravity seemed the wave of the future; Smolin had a chance to start working on it with a top group but declined, and many years later he came to the conclusion that the reason was:
Having learned physics by studying Einstein in the original, I had obtained a sense of the kind of thinking that went into a revolutionary new unification of physics. What I expected is that a new unification should start from a deep principle, like the principle of inertia or the equivalence principle. You would gain from this a deep and surprising insight that two things you had once seen as unrelated were actually at root the same thing…
Supergravity was not doing this. Although it was indeed a proposal for a new unification, it was one that could be expressed, and checked, only in the context of mind-crushingly boring calculations. I could do the math, but this was not the way I had been taught to do science by my readings of Einstein and the other masters
This foreshadows the conclusions of the book as to what is the trouble with physics.
The second part of the book is a very readable history of string theory, explaining the two “revolutions” in the mid-80s and mid-90s, and how they convinced many people that string theory was the ultimate theory of nature. Smolin does not hide the many successes and insights provided by string theory, but does take a more cautelous approach to them that most string theorists would. He expresses frustration, for example, that key points such as perturbative finiteness at all orders, the strong version of the Maldacena conjecture, and the Bekenstein-Hawking entropy of realistic black holes, have not been proved but are commonly accepted as true just because more limited versions of them have been proved. He constantly says that “the pessimist” could take the partial results as nothing more than a coincidence, and that string theorists should not rest in the assumption that these facts are true. These cautionary remarkes may be provide a useful balance against some of the most triumphalist rethoric from the string community, but they are not ultimately very convincing –string theorists who see partial successes as a reason for optimism seem to me perfectly justified.
As everybody knows, Smolin also makes much of the issue of background independence. I certainly agree that the complete theory of quantum gravity ought to be background independent, but my understanding is that string theorists agree as well, and just say that trying to construct from the beginning a manifestly background independent theory is not the most promising route to it, but we ought instead to gain step by step in understanding from the perturbative versions of string theory to the full non-perturbative theory. Now from the LQG camp some will say that pursuing manifest background independence is the most promising approach, and a comparing and debating the archievements and potential of both approaches is indeed legitimate, but the insistence on “background independence” as such a key issue strikes me as a red herring.
Smolin is more convincing when talking about the landscape business, and on his criticism of the anthopic principle. On the latter he concludes, after explaining the situation and providing a list of quotes from famous “anthropicists” including Polchinski and Linde:
There is not a person quoted here whom I do not deeply admire. Nevertheless, it seems to me that any fair-minded person not irratioanlly commited to a belief in string theory would see the situation clearly. A theory has failed to make any predictions by which it can be tested, and some of its proponents, rather than admitting it, are seeking leave to change the rules so that their theory will not need to pass the usual tests we impose on scientific ideas.
Strong words, but I agree that, for the moment at least, anthropic arguments stand outside the boundaries of science. Perhaps if someone came up with a plausible mechanism to bestow a probability distribution on the landscape, together with a plausible definition of the sector of the landscape that allows intelligent life, some testable prediction could be somehow extracted from the approach. But I am extremely skeptical that any of those things will happen in our lifetime.
Some excerpts from the ending of Part 2, after a critical evaluation of how string theory fares at solving each of the Five Great Problems:
String theory succeeds at enough things so that it is reasonable to hope that parts of it, or perhaps something like it, might comprise some future theory. But there is also compelling evidence that something has gone wrong…
So string theory is certainly among the directions that deserve more investigation. But should it continue to be regarded as the dominant paradigm of theoretical physics? Should most of the resources aimed at the solution of the key problems of theoretical physics continue to support string theory? Should other approaches continue to be starved to support string theory? Should only string theorists be eligible for the most prestigious jos and research fellowships, as is now the case? I think the answer to all these questions must be no. String theory has not been successful enough on any level to justify putting nearly all the eggs in its basket.
Part 3 is concerned with those “other approaches” that in Smolin’s opinion deserve as much support as string theory. Its first chapter is about puzzling observational data that don’t fit current frameworks: those supporting the MOND alternative to dark matter, the Pioneer anomaly, the large angular scale anomaly in the CMB data, and others. Next comes a discussion of speculative post-Einsteinian ideas which may be capable of experimental testing soon, the most prominent of which is Doubly Special Relativity. Here I tend to agree with Smolin: the ideas of DSR may prove wrong, but I find them fascinating and deserving of wider interest; especially given that (unlike string theory) there may be hard data coming soon to test them. The third and last chapter of this part explains the “alternative approaches” to quantum gravity: LQG, CDTs, non-commutative geometry, etc. I think Smolin tends to hype the promise of these approaches as much as string theorists do with their own, but (with that caveat in mind) the lay reader will profit a lot from this chapter and the preceeding one, as few popularizations are available on these topics. (Penrose talks about them in The Road to Reality, but how many lay readers can claim to understand half of it?)
Finally, in the fourth part, we get to the practical diagnose and proposed solution to “the trouble with physics”. Smolin finds the root of the problem in the approach to research prevalent in the “elementary particle community”, which continues to be that in string theory, and which he describes as a “brash, aggressive and competitive atmosphere, in which theorists vie to respond quickly to new developments and are distrustful of philosophical issues”. This contrasts with the “relativity community”, whose core values are “respect for individual ideas and research programs, suspicion of fashion, a reliance on mathematically clear arguments, and a conviction that the key problems were closely related to foundational issues about the nature of space, time and the quantum.” Smolin argues that the elementary particle style of research was adequate for the times in which new experimental data were found every other day, but that it is inadecuate to tackle the questions of today, when we have no incoming flux of data to build theories of quantum gravity. In this situation, this style of research leads to fashion-following fads and overcompetiveness with little fundamental progress. After giving many examples in which the string community seems to be falling in “groupthink”, drawing a distinction between “seers” and “craftpeople” (t’Hooft, Penrose and Julian Barbour are paradigmatical “seers”, while it would seem that most string theorists fall on the other side), and going over an interesting discussion on philosophy of science (Smolin is a bit of a fan of Feyerabend) we come to the advice:
We must recognize and fight the symptoms of groupthink, and we must open the door to a wide range of independent thinkers, being sure to make room for the peculiar characters needed to make a revolution. A great deal rests on how we treat the next generation. To keep science healthy, young scientists should be hired and promoted based only on their ability, creativity, and independence, without regard to whether they contribute to string theory or any other established research program. Peopler who invent and develop their own research programs should even be given priority, so that they can have the intellectual freedom to work on the approach they judge the msot promising. (…)
A research program should not be allowed to become institutionally dominant before it has gathered convincing scientific proof. Until it does, alternative approaches should be encouraged, so that the progress of science is not stalled by overinvestment in a wrong direction.
Smolin, in summary, does not so much take issue with the soundness of string theory as physics, but mostly with the way research in it is pursued and the way it is overinvested in in comparison with other approaches. Despite Smolin’s own admiration for Feyerabend, for me it seems natural to put his point in Kuhnian terms: Smolin wishes the area of quantum gravity and fundamental theoretical physics to be treated as a “pre-normal science”, the situation of a discipline before any paradigm becomes dominant and frames the research, as the field of dynamics was before Newton for example. The opposite view that we already have surpassed the pre-normal science stage and have now a paradigm guiding research in quantum gravity, namely string theory, is clearly expressed in Lubos Motl’s comment on a review by Aaron Pierce:
Aaron has an interesting idea that the author of the blue book is really complaining that it is no longer possible for the authors of seemingly fringe theories to get a lot of attention. The book is a lamentation for a bygone era, not an introduction to the field.
(I am not including any new links to Lubos' blog, as a modest and ineffective means to express my outrage at his praise of Augusto Pinochet a couple of days ago.)
Leaving aside Lubos’ usual lack of respect for those who disagree with him, the quote captures quite well the basic disagreement: should we consider that the successes of string theory are strong enough to merit its paradigm status (which automatically makes any other approach a “fringe theory”)? In this key issue I agree with Smolin. Regardless of how impressive we evaluate the successes and potential of string theory to be, it is dangerously unscientific to elevate to this status a theory that seems so far away from any possible experimental confirmation.
However, this does not mean that I necessarily agree with his diagnose and advice to make better progress. I would like to, because I am deeply interested in conceptual/foundational issues and because I have the instinctive dislike that many others share for the fads and fashions prevalent in the string community. (I know a very intelligent young theorist who started studying string theory but abandoned it disgusted by these mores.) But is funding dozens of individual researchers, each with his or her vision of the path to the Holy Grial, a better prospect? It seems to me that lacking experimental input, a focus in conceptual clarity cannot lead to truth anymore than frenetic calculations can. The only example we have in history of a fundamental theory discovered by something like “pure thought” is General Relativity –and it may have been a unique and unrepeatable thing. Moreover, a community of researchers on a subject, even if it is only of five or ten, seems to me necessary to have some standards of intersubjective validity.
The truth is that, insofar as new and unexpected data do not appear, I suspect the situation Smolin decries as a “crisis” will not be overcome. The reason why we are not making progress faster is that we can't build acceperators to probe Plack scale physics and that quantum gravity is very, very hard to develop without experimental clues; the sociological quirks of the string community, if regrettable, play a much smaller role in the explanation. In the meanwhile, we ought by all means to try to develop alternative research programs (preferrably ones that have prospect of connection with experiment (say I, as if that was easy!)). And not put too much energy into semi-scientific anthropic calculations, please.
This book is extremely readable and I would recommended for anyone interested in the present situation in theoretical physics. It is an extremely personal book, much more than most popularizations, so those who are new to the subject should probably balance it with some Brian Greene or Lisa Randall to get a more even view. But the questions it raises about the way science is and should be practised put it beyond the normal popularization and transform into an argument to which members of the field should pay attention, no matter if they ultimately disagree.