Eva Silverstein has a new preprint out, entitled The Dangerous Irrelevance of String Theory. The title is I guess intended to be playful, not referring to its accurate description of the current state of string theory, but to the possibility of irrelevant operators having observable effects.
The article is intended to appear in the forthcoming Cambridge University Press volume of contributions to the Munich “Why Trust a Theory?” conference held back in December 2015. The impetus behind that conference was a December 2014 article in Nature entitled Scientific method: Defend the integrity of physics. In that article, Ellis and Silk explained the problems with string theory and with the multiverse/string theory landscape.
The organizing committee for the Munich conference was chaired by Richard Dawid, a string theorist turned philosopher who has written a 2013 book, String Theory and the Scientific Method. For a fuller discussion of that book, see the linked blog post. To oversimplify, it makes the case that the proper way to react to string theory unification’s failure according to the conventional understanding of the scientific method is to change our understanding of the scientific method. Much of the Munich conference was devoted to discussing that as an issue in philosophy of science.
One aspect of the Munich conference was that it was heavily weighted towards string theorists, with contributions from Dawid, David Gross, Joe Polchinski, Fernando Quevedo, Dieter Lust and Gordon Kane all promoting the idea that string theory was a success. Polchinski explained a computation that shows that string theory is 98.5% likely to be correct, going on to claim that the probability is actually higher: “something over 3 sigma” (i.e. over 99.7%). The only contribution from a physicist that I’ve seen that argued the case for the failure of string theory was that from Carlo Rovelli, see here. Silverstein’s article says that it was commissioned by Dawid for the proceedings volume, even though she hadn’t been at the meeting. I’m curious whether Dawid commissioned any contributions from string theory critics who weren’t at the meeting.
Silverstein begins her article explaining how physics at a very high energy scale can in principle have observable effects. This of course is true, but the problem with string theory is that, in its landscape version, it has a hugely complicated and poorly understood high energy scale behavior, seemingly capable of producing a very wide range of possible observable effects, none of which have been seen. The article is structured as a defense of string theory, without explaining at all what the serious criticisms of string theory actually are. The list of references includes 53 items, only one critical of string theory, the Ellis/Silk Nature article. Some of the arguments she makes are:
It is sometimes said that theory has strayed too far from experiment/observation. Historically, there are classic cases with long time delays between theory and experiment – Maxwell’s and Einstein’s waves being prime examples, at 25 and 100 years respectively… One thing that is certainly irrelevant to these questions is the human lifespan. Arguments of the sort ‘after X number of years, string theory failed to produce Y result’ are vacuous.
I think the comparison to EM or GR is pretty much absurd. For one thing it’s comparing two completely different things: tests of a particular prediction of a theory (EM or GR) that made lots of other testable, confirmed predictions to the case of string theory, where there are no predictions at all. More relevant to the argument over how long to wait for an idea to pay off is that the real question is not the absolute value of the amount of progress, but the derivative: as you study the idea more carefully, do you get closer to testable progress or farther away? I don’t think anybody can serious claim that, 33 years on, we’re closer to a successful string theory unification proposal than we were at the start, back in 1985. I’d argue that the situation is the complete opposite: we have been steadily moving away from such success (and thus entered the realm of failure).
- About supersymmetry Silverstein writes:
In my view, the role of supersymmetry is chronically over-emphasized in the field, and hence understandably also in the article by Ellis and Silk. The possibility of supersymmetry in nature is very interesting since it could stabilize the electroweak hierarchy, and extended supersymmetry enables controlled extrapolation to strong coupling in appropriate circumstances. Neither of these facts implies that low-energy supersymmetry is phenomenologically favored in string theory.
It is true that Silverstein has never been one of those arguing that the usual string theory scenarios with supersymmetry and 10 or 11 dimensions show that string theory is testable. See for instance her comment here back during a “String Wars” discussion in 2006. Her current take on whether string theory implies supersymmetry is just
Much further research, both conceptual and technical, is required to obtain an accurate assessment of the dominant contributions to the string landscape.
The problem with this is that there is no sign of any possibility of progress towards deciding if the string theory landscape implies low-energy SUSY or not (quite the opposite). If you give up the assumptions of SUSY and 10/11 dimensions, you give up what little hope you had of any connection with experiment. She doesn’t mention the LHC at all, especially not the negative results about supersymmetry and extra dimensions that it has produced. The significance of these negative results is not that they disconfirm a strong prediction of string theory, but that they pull the plug on the last remaining hope for connecting standard string theory unification scenarios to anything observable. Pre-LHC string theorists could make an argument that there was good reason to believe in electroweak-scale SUSY, that such a scenario fit in well with string theory unification, and that LHC discovery of SUSY would point a way forward for string theory unification. That argument is now dead. All that’s left is basically the argument that “maybe a miracle will happen and we’ll be vindicated” which in her version is:
In principle one could test string theory locally. In practice, this would require discovering a smoking gun signature (such as a low string scale at colliders, or perhaps a very distinctive pattern of primordial perturbations in cosmology), and nothing particularly favors such scenarios currently.
- Silverstein’s main argument is basically that string theory is valuable because it leads to the study of models that have various observable signatures that people would not otherwise look for. One example here is supersymmetry, the study of which has had a huge effect on collider physics, strongly shaping the analyses that the experimentalists perform. She gives some detailed other examples from her field of cosmology, in particular about possibly observable non-Gaussianities.
String theory participates in empirical science in several ways. In the context of early universe cosmology, on which we have focused in this article, it helped motivate the discovery and development of mechanisms for dark energy and inflation consistent with the mathematical structure of string theory and various thought-experimental constraints. Some of these basic mechanisms had not been considered at all outside of string theory, and some not quite in the form they take there, with implications for effective field theory and data analysis that go well beyond their specifics.
I think this is the best argument to be made for “phenomenological” string theory research (as opposed to “formal” string theory, where there are other arguments). Yes, coming up with new models with unexpected observable effects is a valuable enterprise. If your speculative idea generates such things, that’s well and good. The problem though is how to evaluate the situation of a speculative idea that has generated a huge number of such models, none of which has worked out. At what point do you decide that this is an unpromising line of research, better to try just about anything else? Silverstein makes the argument that
Whether empirical or mathematical, constraints on interesting regions of theory space is valuable science. In this note we focus on string theory’s role in the former.
Since information theory is currently all the rage, it occurred to me that we can phrase this in that language. Information is maximized when the probabilities are equal for a set of outcomes, since one learns the most from a measurement in that case. The existence of multiple consistent theoretical possibilities implies greater information content in the measurements. Therefore, theoretical research establishing this (or constraining the possibilities) is directly relevant to the question of what and how much is learned from data. In certain areas, string theory plays a direct role in this process.
The problem here is that of what is an “interesting region of theory space”. At this point the failures of string theory unification strongly indicate that it’s not such an interesting region. It seems likely that we’d be better off if most theorists focusing on phenomenology of this failed program were to pick something else to work on.
Update: Will Kinney has a Twitter commentary here.
Update: For another relevant recent Will Kinney Twitter storm, see here and here.
Update: Silverstein gave some lectures to the public about this at Stanford recently, video here and here, slides here. A large part of the lectures were an advertisement for string theory, with the summary at the end
Quantum gravity (string theory) plays a subtle but important role, even contributing to our understanding of empirical measurements of early universe dynamics.
Crediting string theory with “contributing to our understanding of empirical measurements of early universe dynamics” is a peculiar way of saying that string theory produces lots of cosmological models that don’t work (see a better summary by Will Kinney at the end of this presentation).
Update: Renata Kallosh is Silverstein’s colleague at Stanford (and Andrei Linde’s wife). In an interview here she makes much simpler and stronger claims about string cosmology than does Silverstein:
string theory ideas help us to build cosmological models which fit the data from observations. Moreover, we have produced relatively simple predictions from string theory and related theories which will be testable with future detectors of primordial gravity waves.
I’m not sure what specifically she is referring to, but suspect that “prediction” here means something like the “predictions” of string cosmology that Kinney describes (see above) whose failure to be observed has in no way affected string cosmologists enthusiasm for the subject.
Update: For some more context about string theory inflation models and the issue of their testability, you could consult Silverstein’s guest post at Lubos Motl’s blog from 2014, explaining how the BICEP2 observation of that era could provide evidence for “axion monodromy inflation”.
“The problem with this is that there so sign of any possibility of progress”
I was invited to write a contribution but declined.
The criticism you raise that there are lots of speculative models that have no known relevance for the description of nature has very little to do with string theory but is a general disease of the research area. Lots of theorists produce lots of models that have no chance of ever being tested or ruled out because that’s how they earn a living. The smaller the probability of the model being ruled out in their lifetime, the better. It’s basic economics. Survival of the ‘fittest’ resulting in the natural selection of invincible models that can forever be amended.
“Historically, there are classic cases with long time delays between theory and experiment – Maxwell’s and Einstein’s waves being prime examples, at 25 and 100 years respectively…”
One has to wonder at the ability of intelligent people to make this type of argument.
Maxwell’s equations validated themselves almost instantly in predicting the speed of light from a number of well established universal constants. Exactly the sort of predictive power that String Theory consistently fails to offer. And Einstein’s GR was validated by Eddington within a very few years, and has been reinforced by just about every test anyone can think of in the 100 years since. Gravitational waves have never been more than a corollary to that. GR has never been reliant on LIGO, like some gravitational equivalent of the LHC, to push its sensitivity ever higher, and ever failing to see what was expected.
I claim neither the intellect nor the background to understand the complexities of String Theory. However, when I see clearly poor arguments and comparisons such as these, then I worry that the complexities are existing on equally weak ground.
You wrote, “I think the comparison to EM or GR is pretty much absurd. For one thing it’s comparing two completely different things: tests of a particular prediction of a theory (EM or GR) that made lots of other testable, confirmed predictions to the case of string theory, where there are no predictions at all.”
Isn’t the real problem the use of the word “theory” to refer both to EM/GR and also to string theory (the same holds for your recent posts on inflation “theory” in cosmology)? Isn’t string theory (again, also inflationary cosmology) more a set of interesting speculations and suggestive calculations that might (or might not) someday lead to an actual theory than currently being a real physical theory?
I know you have made this point again and again, and I do not want simply to be pedantic about vocabulary. But, GR, for example, was sitting there from 1915-16 with, e.g., gravitational waves a definite mathematical consequence of the theory, whether or not anyone could detect them. On the other hand, no one knows what, if any, are the consequences of string theory just because there is, so far, no such theory.
Surely, it would be more accurate to refer to string/superstring “musings” or “speculations” (and similarly for inflationary cosmology). Words do matter.
I think I see a bit more value in such “musings” than you do: I still hope that someday an actual theory will burst forth from all the work on strings. But, alas, not yet.
All the best,
The problem is that usage among physicists has now for a very long time been that the term “theory” carries no implication of testability, being well-defined etc. Unfortunately those trying to defend science against its opponents like to insist otherwise, see for example the Wikipedia entry:
This likely leads many people to believe that “string theory” has characteristics that it doesn’t, but I know of no one trying to do anything about that misunderstanding.
The rather absurd comparison of the testability of string theory to that of EM is surprising to see, but not at all unusual in this kind of document. One would expect an argument being made in an academic context like this to make an attempt to address both sides of the argument, refer to the other side in the bibliography, and not make obviously absurd claims (one question here, are these contributions being refereed?). Instead, what’s produced is heavily ideologically-driven and one-sided. In some sense, I think the worst thing that has happened to theoretical physics over the past 25 years is this descent into ideology, something that has accelerated with the multiverse mania of the last 10-15 years.
Hmm. It doesn’t look like the commenters have read the
…that you left out. This distorts
the meaning and generates like-minded comments
in this echo chamber.
The article goes right on to say in the … that most theories are
not like GR and EM, obviously referring to those
described in the article which are described
rather moderately in the main text. Anyway I
don’t see a problem with a comment about
theoretical predictions predating observations in some
famous cases, and the timescale not being
important, in context of the full article. My
problem is that the space of theories is so large,
so while I do agree that it is quite interesting in
some ways, there’s no way to test
everything in enough detail to infer much
unless we get lucky.
I don’t think anything I left out is relevant or distorts the meaning at all (the only relevant text dropped is “Of course electromagnetism and general relativity are not representative of most theoretical ideas, but the point remains valid.” which I didn’t and don’t see as having any relevance to the point I was making). The problem isn’t that she’s picking unrepresentative theoretical ideas to compare to string theory, or any issue of time-scale, but that she’s justifying the situation of string theory by claiming its like that of one of a heavily successfully tested theory (EM in its early decades).
Peter, the … is about how most ideas will be falsified or
constrained, but that is still valid science, which is a
main theme of the article. The section is about
timescales and null results. You are arguing against
a straw man here — the classic theories were not
compared to string theory, they were mentioned
in the context that even some well established
theories waited substantial periods for certain
of their predictions to be tested, the timescales
for theory and experiment not being perfectly
lined up even in that extreme case. But the paragraph you omitted
makes the contrast quite clear that the author
is making between the two cases. Seriously,
take a moment to consider less incendiary
ways of interpreting and presenting your subjects.
In this day and age, we should all make a point
of being reasonable and accurate.
I think I am being completely accurate and reasonable here. The article is explicitly a defense of string theory against the points made against it by Ellis/Silk, and string theory is explicitly referred to repeatedly in the paragraphs at issue. Claiming that there’s no comparison being made between the current situation of string theory and the situation in the past of EM/GR makes no sense.
The argument of this part of this part of the article seems to me completely straightforward: Silverstein is making the accurate point that it can take a long time to test some predictions of a theory, invoking examples from EM and GR. The absurdity is invoking these particular examples in the context of a defense of string theory research.
Thanks for the very informative links to Will Kinney.
“It is not ever the case that all of a theory’s predictions are empirically verified”
‘True. But it would be useful to have *one*. It would be a start, anyway.”
I think that one comment says it all, really. 😀
I am not convinced you have represented Rovelli’s position correctly. I don’t believe he was a saying that string theory has failed. Perhaps I have misunderstood what you were saying Peter. I think Rovelli was arguing that it had failures such as the lack of black holes, supersymmetry etc at the LHC that should reduce our credence in it. Not necessary cause us to abandon all of its ideas. I don’t think he was a saying that string theory has failed . Perhaps you can point me to the relevant passage if I have that wrong.
Rovelli also seems quite happy with the idea of non empirical verification of science. he says it happens all the time. ” To evaluate theories, they routinely employ a vaste array of non-empirical ar- guments, increasing or decreasing their confidence in this or that theoretical idea, before the hard test of empirical confirmation (on this, see Chapter VIII of ). This is the context of a “preliminary appraisal” of theories, or “weak” evaluation procedures’.
It seems to me then Rovelli is more in the middle between those that say anything that isn’t testable by experiment isn’t science and those that say if its theoretically plausible , that is enough. Im not sure there are many people that take these two extreme views anyway. I think Rovelli is saying non empirical appraisal is part of the scientific process and can give you some sort of “weak” status , a preliminary approval. But only experiment can give you the hard approval to turn your idea from promising proposal to accepted fact.
In Rovelli’s previous appraisal of string theory he has both negative and positive things to say about it. Im sure you know the negatives but the positives were comments like
“String theory is a spectacular intellectual achievement and it might well turn out to be the right track. It is a rich and elaborate theory, that deserves to be studied further…But I think it would be a mistake to consider string the- ory as an established result about nature and therefore concentrate the attention solely on it. Also if the hopes of other research directions are realized, it would be a triumph. String theory appears of unmatched beauty to string theorists, but other ideas appear of unmatched beauty to others. What I think is important is to keep in mind that these theories are provisional.
I am not pessimistic. ”
I am not seeing anything that implies he’s changed his mind about this.
I also think the only game in town comment needs more careful examination. When I interviewed Abhay Ashtekar he seemed to be saying that in one sense LGQ is not a competitor to string theory and in another sense it is. LQG and string theory are both quantum theories of gravity but string theory goes much further in trying to be a unified theory. LQG does not do this and in that sense it is not a competitor to string theory. So I think one needs more care in evaluating the “only game in town” claim. In what sense was it being made ?
When I say “string theory has failed”, I mean specifically failure as a unified theory, not that “one should abandon all its ideas” (of which there are many, of many different kinds). I don’t claim Rovelli would use the same words, but the last three paragraphs of the paper I linked to list “failed predictions” of string theory and argue that that these “lower the degree of belief in string theory dramatically”. I think Rovelli’s “having the degree of belief in a theory lowered dramatically” can reasonably be translated into the more concise “the theory has failed”. Of course “failure” is always something that comes in degrees: what I mean by a “failed idea” is one that is no longer promising. Sure, an unpromising idea may yet get revived, and some people should work on such ideas if they can’t think of anything else to do.
About LQG vs. string theory, sorry but I don’t think that’s relevant to Silverstein’s article.
Peter, I’m not positive, but I suspecct Renata is referring to “alpha attractor” inflation models, which she proposed with Andrei Linde and Diederick Roest in 2013:
It’s basically a class of non-minimally coupled scalar field models with universal behavior at strong coupling. The universality happens at strong coupling because in that limit the scalar sector becomes irrelevant, and the model asymptotically approaches Starobinsky R^2 inflation. In such a case, tensors will be at the r=0.01 level, observable with near-future observations.
Nice model, but calling it a test of string theory is a bit of a stretch, since the exact same prediction can be obtained through suitable choice of potential in a canonical scalar field model, with no reference at all to to UV physics.
The argument “you should not expect to see results in your lifetime” strikes me as identical to the advice given in religious instruction “you should not expect to see end of the world” – which people are hearing now for a third millenium in a row.
You wrote to Peter:
>You are arguing against
a straw man here — the classic theories were not
compared to string theory, they were mentioned
in the context that even some well established
theories waited substantial periods for certain
of their predictions to be tested, the timescales
for theory and experiment not being perfectly
lined up even in that extreme case.
With due respect, I think you are missing the real point here. The problem is not that string theory is a well-defined theory, just as GR was, but that it cannot yet be tested empirically for practical reasons, just as gravitational waves could not be detected for nearly a century.
The problem is quite different: GR was a perfectly well-defined theory by 1916 — it made clear, definite, and unequivocal predictions, even if some of those predictions could not be tested at the time. String theory (like inflationary cosmology) simply is not (yet) a well-defined theory that makes clear, unambiguous empirical predictions.
I.e., the problem with string theory (and inflationary cosmology) is not that we cannot test its predictions due to practical limitations but rather that it does not (yet) make any clear, definite, unambiguous predictions. The distinction is important.
I think Peter’s posts do sometimes give the impression that his objection is simply that the empirical tests of string theory are taking too long in terms of time. But, he has made fairly clear that time is not the fundamental problem: the problem is that there simply is no well-defined, unambiguous theory in existence for strings (or inflationary cosmology).
Maybe that will change. I hope it will, and I am a bit more optimistic here than Peter.
But the distinction is an important one. Whether or not the solution is, as I suggested above, simply to refer to such “theories” rather as “musings” or “speculations,” it is critical to keep in mind a distinction between ideas that make clear empirical predictions that *in principle* can be tested and those which do not.
Linde and Kallosh do seem to have a different definition of “prediction” than most people (including Silverstein, who noticeably doesn’t make claims like this about “predictions of string theory”).
The impression I have about the current state of affairs with “string theory”:
– There is a minority of very vocal senior scientists loudly promoting the string theory landscape multimess on popular media to get publicity.
– The majority of researchers are just trying to mathematically extend “QFT in curved spacetime” in various directions.
The entire mishmash of approaches is mostly lumped together as “string theory” – which isn’t really an accurate characterization.
Would that be approximately correct ?
I’d agree with the first and last part. I don’t think it’s accurate though to describe what the majority of researchers are doing now as “just trying to mathematically extend “QFT in curved spacetime” in various directions”. I don’t think there is any simple way to characterize what “the majority of researchers” are doing, but lots of it has nothing to do with curved spacetime.
Usually I get enraged by such writings, but, seriously now? “Historically, there are classic cases with long time delays between theory and experiment – Maxwell’s and Einstein’s waves being prime examples”?
It’s becoming obvious to me that these people inhabit a very special and distorted space in their mind. Going on with their fervent blind belief and the more and more detached and uselessly sophisticated reasonings just brings them further away from reality — in a very everyday sense of “reality”. Imho I don’t care anymore for the amounts of money and arrest to science’s development that they cause.
Attending pop science events and hearing the audience asking about the multiverse though when the speakers spoke about a dozen other verified wonders still makes me a little sad.
Meanwhile, hope springs eternal for the SUSY folks: https://www.nytimes.com/2017/06/19/science/cern-large-hadron-collider-higgs-physics.html
The problem is that: String theory is not a “theory”, String theory is a paradigm, in the same way as General relativity is a paradigm, once you have a specific model (i mean: a particular solution for the field equations) you could make predictions, notice that if you pick an arbitrary solution form the landscape of general relativity, it is impossible to decide what are good observables, for example: The density parameter is a good number for a cosmological solution, but is irrelevant to try to compute that number for a gravitational wave (an allowed solution). This situation means that general relativity is unpredictable? Of course not and exactly the same happens with string theory, what is the problem with that ?
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