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.
In that sample of 9 high energy theory groups? Yes.
If you’d looked in 1980 (i.e, pre-string), you would have found the same result.
It is a recent innovation (and not an obviously healthy one) to think it plausible that any significant number of people would make a career out of attempting to quantize gravity.
Wheeler, Feynman, and my late colleague de Wit all did many other things, beside their foundational work on quantizing gravity.
As I said above, were string theory not useful for other things (that is, if it were “just” a theory of quantum gravity), it would be highly dubious for the above institutions to employ 4 string theorists, let alone 40.
Given my status as a famous textbook author, I should hope I would be a textbook case.
It looks like I might disagree with Jacques, in that I think quantum gravity really is by far the best justification for doing string theory, and the other stuff is nice while not being central. But I don’t want to damage my rep as a groupthinker.
Here is a reference point on what is happening with four grad students at my school who are interested in particle theory and/or quantum gravity. It is not a representative sample of the theory students; it just illustrates a few ways that the emphasis on string theory affects what grads study.
The school could probably be characterized as being at the upper end of the second tier — it is a good school, but not “top ten.” The physics department is relatively small and probably more progressive in some ways than most schools, so the observations below may not be very representative. The high energy theory group, probably predictably, is weighted toward string theory, with some phenomenology. There is also good interaction with theoretical cosmology. The theorists are very competent and well known in their fields.
The first student I don’t know personally very much, but understand he/she is quite talented and is interested in cosmology and quantum gravity. This person finds loop quantum gravity more compelling than string theory, but there is, predictably, no LQG presence at the school. My understanding is that this person has been offered an opportunity to study LQG at a respected institution elsewhere, so I expect to see one fewer talented grad student around…
The second student is interested in working on both particle theory and quantum gravity, and thinks independently and is willing to consider less conventional approaches if they show promise. This person has seriously considered doing string theory because it is “the only game in town,” but had serious misgivings about it for conceptual reasons. He/she would be interested in looking at LQG more seriously, but as already mentioned that probably won’t happen at this university. More recently he has decided to work in the experimental group on an LHC detector while continuing to spend a fair amount of time on his own ideas; it will be interesting to see whether he ultimately remains in theory.
The third student is currently doing string theory, and will probably do his thesis on a string topic. He always intended to do high energy theory, either string or phenomenology. He was significantly swayed by his observation that some very smart people were doing string theory, and that they were convinced they were on the right track. “That many very smart people probably aren’t all wrong.”
The fourth student is myself. I have also wanted to do high energy theory all along, but also find gravitation very interesting. I am also interested in working on unification physics, but don’t find string theory very attractive. A very important reason is that I don’t see string theory having much interaction with experiment, and I feel strongly that physics theories must be experimentally testable; the requirement that theories be put to a practical test is the fundamental advance of science over philosophy, and empirical tests are ultimately the only way that we can have any assurance that what we believe actually corresponds to “reality.” The other main reason I find string theory unattractive is that it introduces a great deal of baggage, e.g., in the form of extra dimensions and extra particles (I have a related objection to all the new parameters introduced by supersymmetry, which is pretty much required by string theory in my understanding). This is contrary to my belief that unification should lead to simpler models with more constraints than are imposed by the theories we already have, not ones with more degrees of freedom. That may be personal taste, but that’s my taste.
In my view, the best way to proceed toward unification is to understand the standard model better. There are already about 25 parameters to the standard model which are measured experimentally; after that, the standard model is extremely predictive to the point where no known experiments contradict its many, many predictions. Something is obviously very right with it… Still, in the spirit of understanding things better, I, like many other people, think that it should be possible to calculate at least many of those parameters with the help of a better theory. My feeling is that if we had better insight into the origin of those parameters, we would also gain better insight into what issues are important in trying to unify the standard model with gravity. I have some new (and therefore, by definition, unconventional) ideas that I think have the potential to allow calculation of some standard model parameters, and that is where I want to spend at least part of my time. Naturally, this does not mesh well with the research programs at the University… But perhaps surprisingly, the grad committee chair who is a well-known string theorist seems willing to humor me and let me spend half time working on it, at least for a year or so, depending on progress (without RA money, of course, so I’ll still be TA’ing for awhile). My circumstances are not typical in some ways, and this definitely was a factor; additionally, the final details haven’t been worked out yet, so it is not guaranteed to work out that way, although it seems likely.
Those are a few ways that theory students with different attitudes about string theory deal with the “string is king” environment at my school. I am not trying to imply general discontent with the subject — I haven’t seen general discontent with string theory. I’m just trying to illustrate a variety of situations. One string theorist would have graduated this year, but found that finding post-doc positions for string theorists has gotten more difficult, so he is delaying graduation for a year while he keeps looking. I guess things are never easy, no matter what route one takes…
I actually don’t disagree. But the motivations for doing string theory are not precisely the same as the motivations for hiring string theorists.
One of the considerations in hiring (stressed by “pheno” above) is the cross-fertilization with people working in adjoining specialties. For that, the aspects of string theory that you might consider “not central” play an important role. (And, indeed, that was “pheno”‘s point about ‘alternative QG’ theorists.)
Aaron,
The point is that if total funding for theory declines, your “diversity” problem goes away. Instead of funding an alternative, you simply fund less. If you’re funding approaches X, Y, and Z, and you decide that X is overfunded, it doesn’t mean that you must spend the funds that you cut from X on Y, Z or any other alternative.
Ah, Belizean, someone else who has dealt with NASA. I remember the Save Hubble discussions, and I was thinking that if Hubble died then maybe the Beyond Einstein program (next generation x-ray astronomy) could get its funding, but I was quickly informed that it was Hubble or nothing.
Sean, loved the post. I think John B. put it clearly – the question is whether string theory is right or wrong. And I hope that when these two books come out there will be smart articulate string theorists discussing them in print – specifically the reasons why they think Lee and Peter’s arguments against the validity of string theory are not well-founded. Clifford wrote that nice well-written D-brane book so I’m nominating him.
I can see why scientists continue to be excited by string theory, at least right after Maldacena’s paper in 1997 or 1998, even without understanding almost anything about strings, because the connections between the real world and strings are uncanny. It’s like if you can somehow turn an apple into an orange, there has to be some underlying connection or “sameness” between those 2 objects or why would they be able to transmute in this way? So we’ve got to figure out the concept and definition of fruit (continuing the bad simplistic analogy).
Also I wanted to say that in the talks I’ve heard given by string theorists, Joe Polchinski when he gave a colloquium at MIT recently, Gary Horowitz back when I was at grad school (funded by shadowy billionaires, you can guess which coast), David Gross, and many more, they have been up front and not at all defensive about the state of string theory and quantum gravity. At Joe’s last talk on cosmic strings he made it very clear that connection to experiment was needed and we don’t have that. So sociologically speaking I haven’t met any dastardly creatures defending the fortress – well, that is a lie because I just remembered one, a young professor on the west coast, but he drives the string theorists nuts too so, as one of the commenters said, you shouldn’t hold everyone responsible for a few bad apples.
I don’t know Peter, but I do know Lee from his talks and since he’s a high energy theorist I’ll definitely be reading his book. I like Peter’s website though, because whenever he mentions a paper or talk that he takes issue with it’s usually something I’m very interested in reading and unlike him I don’t have my ear to the ground, unfortunately.
Great post and discussion, thanks…
JD says:
True; this is another socioeconomic condition which works in string theory’s favor when it comes to establishing itself in universities. And it is a rational strategy for a university to employ since there are guaranteed benefits even if string theory does turn out to be wrong. And these are the reasons why the taxpayer or benefactor who provides the funding might insist that string theory should be funded rather than the alternatives, even if the experimental evidence favors no particular theory.
But as somebody seems to have raised above, the question really is whether string theory is right or wrong, or even if the statement that string theory is right has any experimental consequences. And I think that I will concur with the consensus of the group Sean declared himself a member of when he said that quantum gravity is the reason why us purists think string theory worth doing.
In addition, if universities want to encourage cross-fertilization, I think it would be great to bring the sociologists and psychologists into the theoretical physics department to see what a fantastic mental mess they’ve made.
But anyway, Jacques, pheno, and I would appear to agree that the motivation for hiring string theorists at present isn’t just to find the theory of everything, or even quantum gravity. If it were, perhaps they could pay a few hermits to scribble nonsense in the attic. But they don’t do that; they hire string theorists.
The answer to Lee’s question about irrational market behavior would then seem to be that the market is behaving perfectly rationally. It’s only irrational behavior if you think the goal is to find the theory of quantum gravity. Resources are being allocated right now in accordance with a set of established priorities, and solving quantum gravity is low on the list of priorities.
So if Sean thought that string theorists have all the jobs, therefore string theory must be overwhelmingly likely, then he should change his mind. The person hiring the string theorist didn’t base his decision on how likely string theory was to be true. String theorists get hired for other reasons.
But it’s not that simple either. Sean’s and Lee’s point of view is more idealistic – money *should* be allocated in such a way as to try to solve the problem of quantum gravity. But the point of view is widespread, and when “The Elegant Universe” is broadcast on the television, I think the idealistic view becomes even more widespread. In fact, I subscribe to this view as well – I think there should be some money set aside for quantum gravity, which will not be spent in accordance with how much it helps some other cause. That money should then be allocated in the most efficient way possible to maximise the probability of finding the answer. Perhaps the government doesn’t want to spend money this way, but some philanthropists probably would.
Just curious.
Are “theoretical mathematicians” by terminology linked to the essence of what the “string theorist” is?
I just found this paper to be helpful in this regard?
pheno grad student,
Since the point of gathering those numbers was to look at what has happened in hiring since string theory hit in 1984, I wasn’t including people whose careers got under way long before 1984. For instance, I wasn’t including Steve Adler at the IAS. Do your numbers also include older people (many of whom never did take up string theory?)
I was also trying to quantify what had happened at the absolute top of the profession, counting those people in the positions of highest influence in the field, thus the restriction to tenured faculty and to the top institutions. Untenured junior faculty at these institutions are a mixed bag, including up and coming young people who will some day get tenure and have a lot of influence, but also often positions where tenure is unlikely, and whose status is closer to that of a senior postdoc.
And again, one of my main points is that these jobs are divided up between string theorists and phenomenologists, with none of them at all going to people working on formal aspects of quantum field theory not related to string theory.
A friend of mine who read this thread asked me to post his comment for him, because he tried and simply could not post it successfully. His name is Hongbao and here is his blog. His comment is quoted as below.
> Einstein is a not a very smart guy.
I disagree strongly on this one.
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Dear Wolfgang,
I think Hongbao actually means that Einstein has great wisdom but not technical smartness. 🙂 Yet this is not my opinion.
Best,
Yidun
They prefer their own theory and viewpoint, however they still keep an open mind to any other approach to quantum gravity. But stringers seem not.
Any number of string theorists have looked critically at LQG. That they didn’t like what they found is not evidence, in and of itself, of close-mindedness.
Dear Lee (to whom this comment is addressed at the first place, but I would be interested to hear anyones thoughts),
First of all let me thank you for your time outlining your thoughts on the social workings in quantum gravity circles in general and the LQG vs. string theory relation in particular.
I am slightly puzzled though by this kind of comparison that assumes that from a high energy physics perspective LQG and string theory are on the same footing and hence a reasonable comparison can be made. If I understand your arguments correctly then you present both LQG and string theory as different approaches to quantum gravity and thus they share the same goal and the difference only lies in the employed methods. If it were such I would agree that a comparison could be made and the results obtained in the two fields could be confronted. However I very much believe that the comparison is not just since string theory is not only an attempt at quantum gravity (regardless of its historical roots or the intention of some of its practicioners) but also a source of numerous insights into conventional QFT (susy Yang-Mills, AdS/CFT, even lattice gauge theory). As a result even if the comparison of LQG and string theory results in some form of judgement (for the purpose of this argument it does not matter which field comes out more favourably in this comparison) in the quantum gravity arena, string theory still has a considerable advantage since it contributed to fields other than quantum gravity as well. On the other hand LQG to the best of my knowledge did not contribute substantially to other high energy physics related fields other than its intended scope, namely quantum gravity.
Thus I am inclined to think that a judgement or comparison of both LQG and string theory can not be complete if it was limited to the field of quantum gravity.
Best wishes,
Xiaofeng
Dear Xiaofeng,
You speak of judgment as if the issue were to choose between LQG and string theory and one had to be sure to be fair. But the issue is not to choose between two theories as if this were a contest for a prize, it is to further the scientific understanding of nature. This means that we investigate promising leads and sooner or later abandon leads that do not lead to predictions by which they are confirmed. We have to think like detectives, not like school officials giving a prize. Moreover the basic ideas beyond string theory and LQG could both be true or both could be false, as they appear to characterize different physical regimes. This is why I personally have invested significant effort on both.
The comparison I did make is between different styles of research carried out by two communities. The two styles existed previously in the difference between high energy theorists and relativists and it is not obvious to me why string theory was embraced by particle physics types and LQG by relativist types-LQG is an outgrowth of ideas and techniques developed to study strongly coupled quantum gauge theories while much of what string theorists actually do is solve the classical Einstein’s equations. My claim is that the relativists’ more foundational and philosophical style is more suited to solving foundational questions and indeed I think string theory would by now have been better understood had this style been adopted by those interested in it.
No one is disputing that string theory has led to fruitful ideas and results about supersymmetric gauge theories. But this does not by itself ensure that it is a true unification because experiment may lead in other directions or it may nevertheless fail-for example, there could be no real non-perturbative formulation of the theory. (As none has ever been proposed this certainly should be considered a significant possibility.) And the fact that a theory also incorporates a hypothesis about unification means that it is more not less vulnerable to failure-because it must get more right. If such a theory makes no predictions at all by which it could be tested then it indeed fails.
Certainly were LQG inconsistent with beyond the standard model unification it would be less likely to be true. But LQG easily incorporates most proposals for beyond the standard model unification including supersymmetry. Furthermore, there is now good evidence that a form of unification emerges from LQG and similar models, see hep-th/0603022. And there is some influence of LQG methods in Freidel’s recent work on solving QCD in 3+1: hep-th/0604185. This is not surprising because the roots of LQG are in the original ideas about loop-field duality in QCD of Migdal, Polyakov, Wilson and others. Conversely, looking back longer, the understanding of how to quantize Yang-Mills correctly came from studies of quantum gravity by deWitt, Faddeev-Poppov and others (ie for them Yang-Mills was studied as an example of a theory with some features of GR.)
Jacques suggests that someone might earn a Clay prize by rigorously constructing quantum Yang-Mills within LQG. It will certainly not be me, but there are people working on exactly that program. The conjecture is that background independent QFTs are more likely to exist rigorously in 3+1 dimensions than Poincare invariant QFTs. After all, there is gravity in the world and, with the exception of the existence and uniqueness theorems in LQG, no one has succeeded in constructing a rigorous QFT in 3+1. Since Jacques is in favor of people jumping into hot topics to make them go faster perhaps he might want to jump into that. We would welcome his contributions.
Thanks to everyone for the high level of the discussion here.
Lee
Ah. What a breath of fresh air! Actual physics content.
“Most”, but not all?
What sorts of quantum field theories can be incorporated, and what sorts cannot?
In the real world, the QCD scale is 19 orders of magnitude smaller than the Planck scale (for theoretical purposes, it might as well be 1000 orders of magnitude smaller). I don’t see how coupling to quantum gravity is supposed to make any of the problems of constructing Yang-Mills theory easier.
But I wish your colleagues the best of luck …
Ah, yes, the “LOST Theorem”. We really ought to have a discussion about that sometime …
Come on Sean, You know very well if a graduate student in high energy theory is working on something new or something non-stringy, she reduces her chances of getting a post-doc by 100 times. Because people who are hiring are all string theorist and are looking for these specialized skills, not general creative ability. (may be just because the technology involved is highly specialized) Such a thing does not exist in say cosmology, where new directions taken by graduate students will be rewarded.
Hello to all,
Great blog.
The foregoing (I’ve read a nontrivial chunk, perhaps 20%), though interesting, vindicates my decision 25 years ago NOT to become a professional physicist.
It appears possible to me that the whole field of physics is barking up the wrong tree – or perhaps simply that the “right tree” is neither cosmically large or infinitesmally small enough to be deemed worthy of a theoretical physicist’s attention.
Maybe the “right tree” isn’t even physical. Maybe the word “physical” has outlived its usefulness in this context.
I found myself writing on something tangentially related to this subject just a few weeks ago.
Listen to the Moon
Listen to the Moon
Regards,
theOwl
Dear Lee,
Thank you very much for your thorough reply, I’ll try to respond to the points you raised.
You write
“No one is disputing that string theory has led to fruitful ideas and results about supersymmetric gauge theories. But this does not by itself ensure that it is a true unification because experiment may lead in other directions or it may nevertheless fail-for example, there could be no real non-perturbative formulation of the theory.”
and I fully agree with that. As long as experimentally relevant predictions, true description of nature is concerned (which are undoubtedly very ambitious and important goals) a theory can be right or wrong and consequently both string theory and LQG can be right or wrong on the end of the day. These ambitious experimentally relevant issues include quantum gravity, unification, physics beyond the standard model.
However if we can afford to be less ambitious — and why should not we for a moment when we are facing difficult problems — then we may label a theory ‘good’, useful, insightful or by other generally positive adjectives along these lines based on slightly less ambitious goals, namely if it provides insight and results in other high energy physics fields. You may ask how one can quantify these results and insights if not by experimentally relevant predictions and falsifyability. To that I would respond that these results and insights are in the conceptual framework of toy models which are not directly relevant for experiment but nevertheless further our understanding of nature. As an example, very few of us would agree that the work invested in the study of 2 dimensional exactly solvable and integrable systems constitute a ‘failure’ or are useless in general just because they do not directly describe physical phenomena and produce testable predictions. They are not promoted to be experimentally relevant physical theories but they are still useful and insightful; classic examples of toy models.
Thus I am inclined to 100% agree with you that at the moment string theory provides zero experimentally relevant predictions and thus does not stand the test of a true physical theory describing nature, however the amount of insight string theory provided for conventional QFT (of the type that can be considered toy models of the real world) already justifies the claim that string theory is ‘good’, useful and insightful and definitely not a failure. These results are a consequence of the working style, habit, attitute, etc. of the string community (including you and others of course who are not string-only but nevertheless contributed to the subject) thus this working style, habit, attitute must be credited for what it achieved. It did not produce a physical, experimatenally relevant, testable theory, true, nothing to hide there, but it did achieve important insight nevertheless which should not be overlooked.
LQG also provided insight into other high energy physics fields some of which you mentioned in your post but these insights are also in the arena of toy models, that is LQG also failed to make testable, experimentally relevant predictions so far.
I also understand that over-ambitious claims of some string theory practicioners can be troublesome (“theory of everything”, “unification of all forces”, “unique description of nature”), however these claims carry no weight in a scientific discussion, only the results themselves. Clearly these claims are not justified from the point of view of the actual results since string theory did not achieve anything along these ambitious lines, but the balanced response should not be a total rejection, but only a lowering of the expectations, especially if the lowered expectations are still very high. Not as high as it could idealy be, but still good enough to justify research in this direction. In this perspective I fully agree with David Gross saying “string theory can not be wrong”, since the contrary would be analogous to saying “toy models are wrong”.
In my opinion one should resist the temptation to be cynical about this lowering of expectations and resist saying “haha, they thought they can do everything and they can do only a small portion of that” especially if that small portion is quite substantial.
Since you say that the current question is not about a mutually exclusive choice between string theory and LQG I will not attempt to compare the toy model related results of LQG and string theory but limit myself to a conclusion keeping in mind your main argument, namely the style of research, whether a “more foundational” or some other style is desirable. The “string theory style” already showed its strength in studying toy models so I do not see a reason to abandon this style, especially if the competing style, the “more foundational style” can claim victory neither for experimentally relevant predictions nor for toy models.
Best wishes,
Xiaofeng
– Lee Smolin
Well mathematical rigor and physical predictions can be two different things. (Rather that someone wins a Nobel Prize for physics than a Clay Prize for math.)
I would like to see a clear physical description of the LQG spinfoam vacuum, one that can compete with string theory in popular understanding. In a LQG for a Yang-Mills theory, the loop consists (presumably) of the cycle of gravity causing gauge boson radiation from the Higgs field giving one mass to that of another mass, and back again to the first mass? Is gauge boson radiation redshifted by cosmic expansion? Would that weaken long-range gravity without requiring a repulsive dark energy in the Lambda-CDM model? Is this a checkable prediction?
theOwl:
Your entire life is a gift from these physicists that seem like “barking up the wrong tree” to you.
Try saying this to a medical physicist when you go for an MRI, an X-ray etc.
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Owl, with all due respect to John Wheeler, (which is a lot!), you’d have to be independently wealthy to think that we are here to “observe” the universe into being.
He must’ve missed the guy working the jackhammer…
Lee writes:
LQG is an outgrowth of ideas and techniques developed to study strongly coupled quantum gauge theories
Funny, in studying strongly coupled quantum gauge theories, usually the first thing one would like to check is that the continuum limit exists. In other words, there should be a fixed point (perhaps Gaussian) with finitely many relevant perturbations. As I understand it, LQG has not yet demonstrated something like this for gravity.
This is not surprising because the roots of LQG are in the original ideas about loop-field duality in QCD of Migdal, Polyakov, Wilson and others.
Most of us would say that this loop-field duality has been fully realized, in a very deep way, by string theory. The AdS/CFT correspondence, and its generalizations, are a beautiful example of how the gauge theory can be described in terms of Wilson loops. These Wilson loops have finite thickness, which translates into a the necessit for the holographic dimension. The holographic dimension also encodes renormalization group flow. It’s a beautiful, unifying description of various ways to look at gauge theories, and it came from string theory.
String theory also has a deep, organic connection to strongly-coupled gauge theory, whereas you seem to suggest that it is merely concerned with the perturbative realm.