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.
I do not know a lot about string theory beyond the Elegant Universe, but I do know bandwagons and hypes (I work in quantum information theory). Hypes are largely generated in the media, who latch on to specific results, even though their popular representation might not be completely correct (“string theory predicts gravity”, “quantum computers are superfast”). There is then a feedback mechanism that may turn a hype into a bandwagon.
Still, the bandwagon needs to be pushed along. The fact that there is a hype is a sign of a healthy discipline (both in terms of results and funding). Even the size of the backlash is a measure of the success of string theory.
I think the whole issue of hype misses an important point. ‘Hype’ to me implies some disingenuousness. NBA picks, for example, are hyped by agents in the hope of increasing the paycheck later on. What people call hype in physics, I see as people being excited about their work. People are in physics because they think it is fun, and they want to share their new ideas. There is an inevitable distortion coming out of this, but it isn’t restricted to string theory. LQG, braneworlds, ekpyrosis, etc. have all gotten their articles in the Science Times, too. Science journalists are trolling the arXiv for the next new thing, and most scientists are willing to talk to them. Maybe in a better world, all such articles would have their needed share of caveats, but that doesn’t make the greatest copy. In the meantime, I tend to think that people being excited about their work and wanting to share their ideas is overall a good thing,
Thanks for a good post, Sean. For my part, I got excited about string theory after reaching grad school and worked awfully hard for the chance to work in the field. I won’t say that nobody has ever felt “trapped” into doing strings, but that notion is entirely foreign to my experience.
The thing that has always puzzled me about the “string backlash” is what exactly string theory’s detractors would like to see string theorists do differently. (I am happily ignorant of any “reprehensible” tactics used by anyone in the debate, so of course these comments apply only to the overwhelming majority of decent people out there.)
Do they want us to leave the field? We won’t, not until we find another idea more compelling. (And if it turns out to be wrong, hey, it’s our careers on the line, not theirs.) Do they want us to stop telling the public about our work? We won’t: public outreach is part of science, and sharing things that one finds exciting is part of being human. Do they want us to make it clear when we speak that our work is tentative and not yet verified by experiment? We already do. Or at least, I always emphasize it, and most of the string talks that I’ve seen do the same. (We don’t include disclaimers on every slide,of course!) What more do they want from us?
In the end, I find the “backlash” rather frustrating. I’m just following the physics I find most interesting, and somehow that generates not just scientific objections but what feels like actual resentment. I’m glad to have “lots of smart physicists” doubting string theory and pursuing other ideas that they consider promising! Why should I have to convince them to abandon those other possibilities entirely (by convincing them that strings are “on the right track”) before they will cease what feels like active hostility?
Why do we need popular science books dedicated (or half-dedicated) not to sharing some exciting new idea but rather to cutting one down? Has anyone written a popular science book that’s mostly about why, say, technicolor is wrong? Or about why the resonant valence bond model of high Tc superconductivity is wrong? What makes string theory such a unique target for this sort of broad public criticism?
MoveOn, it is statements in your comment, such as:
that keep this endless discussion irritating rather than substantive. Quite frankly I am tired of string folks spouting that any other area of particle theory is simply not good theoretical science (yes, I’ve had some string theorists say this to my face). It grows tedious when one resorts to name calling in a debate rather than basing their position on facts.
As to whether string theory is correct or not, the science will eventually decide, as Sean says. Personally, I think it is rather conceited of us to think that we are special enough to be able to accurately extrapolate 16 orders of magnitude – without any knowledge of the science that takes place within that energy range – and be able to describe nature at the Planck scale. Doesn’t mean that we shouldn’t try – we learn alot by trying – but we need to keep our feet on the ground while doing so.
Speaking of hep-ph, there is much excitement there these days with alot of stimulating model building, breathtaking tour de force higher order calculations, collider physics is energized, there is a new level of precision in lattice calculations, and new effective theories being developed to describe heavy flavor interactions. All of this work is developed under the arduous constraints of being consistent with the full global data set – I can tell you that is not trivial. All of this work is also developed knowing that it will be tested and proved right or wrong soon. Very soon.
Lastly, for all future Princeton graduate students who would like an alternative to string theory, I note that Lian-Tao Wang – a talented collider phenomenologist – is arriving as an Assistant Professor this Fall.
Excellent post Sean, I think you are right on the money in highlighting this interesting issue, even people who do not care much for string theory would probably not like the self-managing style of the scientific community compromised in any way.
Steuard, my sentiments exactly.
JoAnne: the list you make is really interesting, I don’t recall any of these issues discussed in popular or semi-popular press, but of course with blogs one does not need those…
Dear Steuard,
Yes, you may not need those public science books that are against string theory. However, the whole society needs them, the society needs different voices. In fact, you are doing something of impelling interest only to you and a group of people. The theory you are working on is still under development. There is not solid evidences showing that it will be ultimately true. Moreover, since you think advertising the theory to the public is part of the science, why couldn’t you allow others to have opposite points of view? And those others are scientists as well. Actualy, the more an approach is advertised, the more criticism it’ll receive.
If you are working on some well established physical areas, you may get less criticism for sure. From my humble viewpoint, however, a theoretical physicist who works for his own dream should not be afraid of criticism, public or private, as longs as those criticisms are scientifically rational but not emotional, because they are healthy for our scientific air at all.
I would apologize if I misunderstood any of your points.
Best, Y.
From a layman who works hard to understand.
Not that it matters, but seeing “in the ways” Jacques continued efforts to educate and speaks about, is refreshing reminder of the strange world you scientists are working in.
“Dynamical triangulation” John? :)Monte carlo models, to flipping on quantum gravity methods?
I have not heard to many from the likes of Steuard, who give their opinion on it from the inside. The talk Mark relayed on “negativity” would have been a good thing, if the insight and opinion were given from scientific stance, as was the discussion linked to cosmic variance, by Jacque in “I.”
Aaron and Lee rebuttals, as well as the stand Peter Woit and Lubos(I won’t hold character against anyone as long as their willing to share perspective?) took to debate the sustenance string theory has for the future? Did character from either hurt this move to debate from a “negative stance” reveal other information? 🙂
Creating the situations for advancing our understanding. How appropriate 🙂 Supersymmetry conference, Anthropic debate, etc. Advancing the positions of all who understandly speaking from their respective models, who know, that such a forum may have initiated new ideas?
I think laying aside the “conspiracy theory” would be a good thing.
Oh Yes, this is a good post too Sean.
JoAnne,
Whenever you have some time, would you mind telling us more about the breathtaking tour de force higher order calculations and the new level of precision in lattice calculations?
Thank you!
Moshe wrote:
Agreed. I certainly hope so. But I fear the hope is unrealistic. So far the natural sciences had objectivity on its side, so the funders of science were content to let this be so. The facts spoke for themselves. If the main justification for a line of research is that a lot of smart people think it worthwhile, then the hands-off attitude may change.
Why do you think journalists don’t write articles about the questions that motivate quantum gravity theorists? There’s not much data available right now, so it’s not a good time to be writing articles explaining the nature of the universe; scientists have many useful partial explanations, but our whole picture doesn’t hold together yet. We’ve got some neat hints though, so it’s a great time to ask questions. That’s really where most of the fun in quantum gravity is anyways: in wondering, for example, why black hole entropy doesn’t seem to scale with volume. (That susygravity and strings offer a framework for asking questions of this form is one of the things that makes it interesting to theorists. That it makes it comparatively easy to do so is cause for celebration or suspicion, depending on your levels of cynicism. 🙂
But there are some good science articles to be written about the questions in quantum gravity. And it’d probably give people a better idea how science works and what theorists do during the day, aside from posing in white labcoats.
i’d just like to 2nd arun’s post #33 above asking joanne to tell us about some of the phenomenology being done at the moment. it seems like a lot of the particle theory blogosphere is string-based (i know this isn’t 100% true), it would be great to hear about theoretical work being done that is more closely tied to experiment (tevatron, lhc etc,).
“‘Hype’ to me implies some disingenuousness. NBA picks, for example, are hyped by agents in the hope of increasing the paycheck later on. What people call hype in physics, I see as people being excited about their work.”
As a counterexample, I offer to you Professor Michio Kaku. Highly disingenuous by any standard (I’ve heard him on the radio), and he has a clear paycheck motive: hawking books and various media appearances.
I suppose you could argue that he’s not a real practicing physicst, he just plays one on TV.
I suppose you could argue that he’s not a real practicing physicst, he just plays one on TV.
Yeah, pretty much.
I second the comments of JoAnne above. I’d be the last person to suggest that both serious model builders and phenomenologists have not been greatly (and positively!) influenced by ideas that arose from string theory. Hell, my last paper was on signatures of extra-dimensional, non-commutative Tev-scale black holes at the LHC. But there is much, much more to phenomenology than this. Overall, it is a very broad yet under-valued field and has been for some time, since the death of the SSC back in ’93. Many of us have had some of the same bad experiences that JoAnne mentioned re the interactions of stringers and phenomenologists. There is some sense that this is changing perhaps due to the advent of the LHC next year.. particularly when you talk to the younger graduate students. I hope so..for the sake of the future of our field…but it may all depend what happens at the LHC.
Perhaps we’ll have this conversation again in 2010-11.
This is all rather tiresome. Why is there so much vitriol directed at string theory? For understanding the theoretical underpinnings of quantum gravity and cosmology, most physicists who have thought about it have decided it’s the best answer. If people want more physicists working on “alternatives” like LQG, they should go into LQG and produce interesting results to persuade people to switch, not rail against some imagined injustice. The fact is, many physicists have, at least briefly, looked into LQG and decided it is not interesting. The reason is quite clear, when you look at, say, Lee Smolin’s comments on Peter Woit’s blog, where he was totally unable to provide any explanation of how (or whether) LQG matches onto a unique low-energy Wilsonian action reducing to Einstein gravity in the IR, and evaded the question with wishful thinking that “deformed special relativity” would somehow enforce renormalizability. If someone has a true alternative and can sensibly answer basic questions about how it overcomes long-standing problems, people will notice and take interest.
A nice topical post, Sean. I agree that good alternatives need to be built before people should take them seriously. How long will that take? Who knows?
Aaron,
Yes, hype implies disingenuousness to me, too. I’ve been involved in (and observed on blogs) plenty of arguments involving string supporters that were loaded with hype. For example, certain string supporters will not admit that the current state of string theory does not allow one single prediction to be made. Despite this complete lack of experimental support, the most lavish claims are made about string theory. That I would call hype.
Of course, I am not suggesting that you personally engage in hyping the theory, Aaron. I find your comments to be quite reasonable.
I also agree that other ideas are hyped, but none more than string theory. And this brings me to Steuard, who asks what string theorists ought to do differently. No, I don’t want you to stop doing string theory. No, I don’t want you to stop communicating with the public. But please have some perspective when communicating with the public.
Rather than oversell string theory, as is often done, this is a wonderful opportunity to let the public in on how science develops. Bend over backwards to let the public know that this is a theory in development , and that there is no experimental support yet, so that it is extremely tentative. Emphasize that the foundations of the theory are not well-established, but that we are groping around in the dark, trying to find fruitful ideas. Let the public know about some of the most difficult unsolved problems that are currently occupying researchers, don’t just try to impress them with higher-dimensional razzle-dazzle. Let them know how murky and difficult is the task of theory-creation, and they might catch the excitement of science too.
From the post:
Sean,
Could you explain more fully why the appearance of this rich structure—the AdS/CFT correspondence—is taken as an indication that string theory is on the right track? What reasons do we have, independent of string theory itself, to suppose that this rich structure is of physical, and not just mathematical, significance? Certainly it indicates that field theory can be recast (with certain caveats) in a very different form, but what does this really mean for physics?
Arun & Bizarre: you bet! I’ve been completely snowed under the past few months and somehwat neglecting my blogging duties. However, this summer is looking better and I will do a series of posts on the current excitement in particle phenomenology.
Let me propose two completely compatible statements:
1) String theory is the most promising route for unifying gravity with other fundamental forces.
2) Trying to unify gravity with other fundamental forces is NOT the most useful way for most particle theorists to spend their time, since the lack of experimental predictions, massive extrapolation in energy, and top-down approach impede real progress.
Steuard,
“Why do we need popular science books dedicated (or half-dedicated) not to sharing some exciting new idea but rather to cutting one down?”
String theory is not an “exciting new idea”, it’s one that has been around for nearly 40 years, and for the last 22 years has completely dominated particle theory and consumed much if not most of the resources dedicated to the subject. It’s long past time for an honest evaluation of what results have been achieved by all this work, and what the prospects are for future progress.
“Has anyone written a popular science book that’s mostly about why, say, technicolor is wrong? Or about why the resonant valence bond model of high Tc superconductivity is wrong? What makes string theory such a unique target for this sort of broad public criticism?”
The other ideas you mention haven’t been overhyped for twenty-two years, and been the subject of an endless and ongoing flood of popular books, radio and TV programs while getting ever farther and farther away from any success or contact with the real world. The ratio of amount of effort and hype that has gone into string theory to actual progress towards its stated goal (unification of particle physics and gravity) is enormous and historically unprecedented.
The story of what has been going on in particle theory over the last quarter century is one that deserves at least one or two books that approach it in some other fashion than through over-enthusiastic repetition of what the hopes for string theory have been, books that acknowledge that these hopes haven’t worked out and examine why. John Baez is right that one important thing that my book (and Lee’s, I gather) do is to lay out in detail what the scientific argument is that string theory-based unification hasn’t worked and most likely can’t work. It’s a complicated subject, not suited to a summary in a blog comment. I look forward to discussions about it with any string theorists willing to actually read what I have to say, rather than to just complain about the fact that I’ve chosen to say something they don’t want to hear.
Jacques Distler writes:
Last fall, I wrote a series of posts (I, II, III) which I hoped might be a springboard for exactly the sort of sober discussion you’re talking about.
I’m still surprised at how little disagreement there was in the responses. I was hoping that someone would pipe up and explain why I was wrong.
The first of your posts is dated September 1st, 2005. By chance, it was the day before, August 31st, that I wrote an issue of This Week’s Finds where I said I was sick of thinking about quantum gravity. So, that’s my excuse for not joining that discussion. But, thanks for tackling some of the big issues.
I’m still sick of thinking about quantum gravity. Someday someone will figure it out, but not me.
Chris W. — What I said was that it “keeps people optimistic,” which I think is accurate. It’s not just that the theory can be written in various different forms; it’s that those various forms are reminiscent in interesting ways of the real world. The bad news about string theory is the lack of detailed confrontation with experiment; the good news is that, even without such help, we’ve still learned a remarkable amount about the theory (and about ordinary field theory).
Admittedly, it could very well be all just an accident, and the fact that N=4 super Yang-Mills is dual to a ten-dimensional theory of gravity could have nothing to do with the fact that there is gravity in our real world. But string theory could have simply gotten stuck in the 70’s after people realized that it predicted a massless spin-2 graviton, and it very definitely hasn’t. People keep discovering new and unanticipated features of the theory, which is taken as a clue that it might be on the right track. It would be a shame, in some sense, if all that tantalizing structure were there, so obviously related to things we observe in nature (gravity, gauge theories, etc), and yet it all just be an accident. Clues are no substitute for hard evidence, of course, so we’ll have to keep plugging away.
Re: the lack of respect for phenomenologists among string theorists. I’ve known alot of string theorists, and one belief that I have found almost universal is that if phenomenology ever becomes “interesting” again, they (the big-brained theorists) will be able to jump right in, thank their smaller-brained phenomenologist friends for keeping the bench warm, and start cleaning up in the phenomenology business. Admit it! I’m talking to you Shamit! Personally, I think they’re fooling themselves.
How does one get on these free book distribution lists, anyways? I’d be happy to say something about either book, but I can’t see myself shelling out 27 bucks a pop for the things.