In October 1984, it was announced that the Nobel Prize for Physics had been awarded to Carlo Rubbia and Simon van der Meer, for the discovery of the W and Z bosons at the UA1 experiment at CERN just the previous year. This was the capstone discovery in the establishment of the Standard Model of particle physics. The third generation of fermions had already been discovered (the tau lepton by Martin Perl in 1977, the bottom quark by Leon Lederman also in 1977), and the nature of the strong interactions had been elucidated by deep-inelastic scattering experiments at SLAC in the late 1960's and early 1970's. Unsuspected by many, particle physics was about to enter an extended period in which no truly surprising experimental results would emerge; subsequent particle experiments have only been able to confirm the Standard Model over and over again, including the eventual discovery of the top quark at Fermilab in 1995. (Astrophysics, of course, has provided substantial evidence for physics beyond the Standard Model, from neutrino oscillations to dark matter and dark energy.) A month earlier, in September 1984, Michael Green and John Schwarz submitted a paper on anomaly cancellation in superstring theories. String theory had been around for a while, and it had been understood for ten years that it predicted gravity, and was a candidate "theory of everything." But there were many such candidates, each of which had run into significant difficulties when taken seriously as a theory of quantum gravity. Most people who were paying attention had presumed that string theory would face the same fate, but the Green-Schwarz result convinced them otherwise. A brief article in Physics Today was entitled "Anomaly Cancellation Launches Superstring Bandwagon," and theorists everywhere jumped to learn everything they could about the exciting new possibilities the theory offered. So here we are, over twenty years later, still with no surprising new results from particle accelerators (although hopefully that will change soon), and still with strings dominating the landscape (if you will) of theoretical high-energy physics. And still, one hardly needs to mention, with no clear path to connecting string theory to low-energy phenomenology, nor indeed any likely experimental tests of any sort. In the circumstances, it's not surprising there would be something of a backlash against string theory. The latest manifestation of anti-stringy sentiment is in two new books aimed at popular audiences: Peter Woit's Not Even Wrong: The Failure of String Theory and the Continuing Challenge to Unify the Laws of Physics, and Lee Smolin's The Trouble With Physics: The Rise of String Theory, The Fall of a Science, and What Comes Next. I haven't read either book, so I won't presume to review them, but I think we've heard the core arguments expressed on this blog and elsewhere. I'm a firm believer that it's good to have such books out there; I'm happy to let the public in on our internecine squabbles, just as I'm happy to keep them updated on tentative experimental results and speculative theoretical ideas. It seems unduly patronizing to think that we can't reveal anything to the wider world until everyone in the community agrees on it. But I don't actually agree with what the books are saying. Here is the main point I want to make with this post, trite though it may be: the reason why string theory is so popular in physics departments is because, in the considered judgment of a large number of smart people, it is the most promising route to quantizing gravity and moving physics beyond the Standard Model. I don't necessarily want to rehash the reasons why people think string theory is promising -- I'm not positing an objective measurement of the relative merits, but simply an empirical observation about people's best judgments. Rather, I just want to emphasize that, when you get right down to it, people like string theory for intellectual reasons, not socio-psycho-political ones. It's not a Vast String Theory Conspiracy, funded by shadowy billionaires who funnel money through Princeton and Santa Barbara to brainwash naive onlookers into believing the hype. It's trained experts who think that this is the best way to go, based on the results they have seen thus far. And -- here's the punchline -- such judgments could change, if new results (experimental or theoretical) came along to suggest that there were some better idea. The way to garner support for alternative approaches is not to complain about the dominance of string theory; it's to make the substantive case that some specific alternative is more promising. (Which people are certainly trying to do, in addition to the socio-psycho-political commentating about which I am kvetching.) That is, after all, the way string theory itself became popular. Green and Schwarz labored for years on a relatively lonely quest to understand the theory, before they were able to demonstrate anomaly cancellation. This one result got people psyched about the theory, and off it went. It's not a matter of impressionable young physicists docilely obeying the dictates of their elders. Read Jacques Distler's (absolutely typical) story about how he dived into string theory as a graduate student, despite the fact that his advisor Sidney Coleman wasn't working on it. In a completely different field, listen to Nobel-winning economist Gary Becker on the response to his ideas (via Marginal Revolution):
"There was a sea change. I began to notice it in the 1970s and 1980s. A lot of the younger people coming out of Harvard, MIT and Stanford were very interested in what I was doing, even though their faculty were mainly - not entirely - opposed to the sort of stuff I was doing."
This is just how academics act. They are stubborn and willful (even at a charmingly young age!), and ultimately more persuaded by ideas than by hectoring from their elders. And it's not just the charmingly young -- if good ideas come along, supported by exciting results, plenty of entrenched middle-aged fogeys like myself will be happy to join the party. If you build it, they will come. There's no question that academic fields are heavily influenced by fads and bandwagons, and physics is no exception. But there are also built-in mechanisms that work to protect a certain amount of diversity of ideas -- tenure, of course, but also the basic decentralized nature of university hiring, in which different departments will be interested in varying degrees in hiring people in certain fields. Since the nature of science is that we don't yet know the right answers to the questions we are currently asking, different people will have incompatible intuitions about what avenues are the most promising to pursue. Some people are impressed by finite scattering amplitudes, others like covariant-looking formulations, others don't want to stray too far from the data. The thing is, these considered judgments are the best guide we have, even if they are not always right. Green and Schwarz were lonely, but they persevered. If you want to duplicate their success, find a surprising new result! You can't ask a department to hire people in an area they don't think is promising, just because it serves the greater goal of diversifying the field overall. Crypto-socialist pinko though I may be in the political arena, when it comes to intellectual life I'm a firm believer in the free market of ideas, and would tend to resist affirmative-action programs for underrepresented theories. The bandwagons come and go, influenced by both data and new ideas. When I was in grad school in 1990, things were in a lull in fundamental physics generally, and students were escaping to Wall Street and elsewhere. The discovery by COBE of temperature anisotropies in the microwave background re-invigorated cosmology, and attracted a number of bright young theorists. The Second Superstring Revolution in the mid-90's did the same for string theory. There's every reason to believe that the LHC will do the same for phenomenology -- the leading indicators are already easily visible. The thing that has kept string theory alive is that interesting results have kept coming, from the 70's (gravity!), to the 80's (anomaly cancellation, five critical string theories), to the 90's (branes, dualities, black hole entropy, AdS/CFT). The last few years haven't witnessed their own "revolution" (unless you count the landscape), but it would seem a little impatient to give up on that basis alone. If nothing else, string theory is extraordinarily fruitful and robust. Indeed, the AdS/CFT correspondence says you can't really separate field theory and string theory. Take an ordinary gauge theory in flat four-dimensional spacetime, and make it as supersymmetric as possible without adding gravity. Then make the coupling very strong, and the degrees of freedom rearrange themselves -- just as the strong coupling in QCD makes the quarks and gluons rearrange themselves into pions and nucleons -- into Type IIB superstrings living in a ten-dimensional spacetime. How amazing is that? It's not proof that strings are connected to the real world (which, as people sometimes forget, is not manifestly maximally supersymmetric, and does in fact involve gravity), but it's the kind of rich structure that keeps people optimistic that string theory is on the right track. Of course, you do have to make the case that your personally favorite approach is a promising one, to the public and to colleagues in other specialties as well as to graduate students. This is not always a job that string theorists have done well. Some of them, I've heard rumors, can even occasionally be a mite arrogant. Let's admit, this is something of an occupational hazard among academics; if universities fired all the arrogant people, the remaining faculty would be stuck teaching twenty courses a semester. And, while I think that an enormous landscape of stringy vacua might very well exist, I think that supporters of the idea have dramatically failed to take seriously the difficulty of actually calculating anything on that basis. Discussions about these crucial issues have all too often degenerated into sophomore-level philosophy-of-science debates, which haven't done credit to either side. The truth is, we're not doing science in a new way, it's the same old way -- trying to come up with the simplest possible consistent and coherent framework that explains the phenomena we observe. And (to add one more "of course"), needless to say we need to keep our eyes on the prize, which really is explaining those phenomena. Sometimes people do get entranced with the math, which is fine, but as physicists the ultimate arbiter of interestingness is a connection to data. String theory hasn't done that yet, and might not do it for a long while, but in the end will have to, one way or another. It's hard! But string theory will either progress to the point where its connections to reality become increasingly manifest and specific, or people will lose interest and work on other things. That's the way the system works. Update: Interesting reports from the Strings 2006 meeting in Beijing from Victor Rivelles, Jonathan Shock, and Dennis Overbye.
