Why String Theory?

I recently got a copy of Joseph Conlon’s new book Why String Theory? and was pleasantly surprised to find that it’s quite good. Conlon is a lively, entertaining writer, generally sensible about the scientific issues involved, and I think does a great job of explaining the point of view of typical physicists now working on string theory. He also very ably explains the “sociology” of the field, the different kinds of people who work in this area and their varying sorts of goals and motivations.

The book is explicitly motivated by the desire to answer a lot of the criticism of string theory that has become rather widespread in recent years (wasn’t always so…). For a typical example from the last few days, see Why String Theory is Not a Scientific Theory at Starts With a Bang. I have mixed feelings about this sort of thing. It gets the main point quite right, that string theory unification is untestable, having failed to make any predictions, and by the conventional understanding of the scientific method, it’s past the time at which most theorists should have abandoned it and moved on. On the other hand, I don’t see at all the point to arguing about the term “scientific theory”. Sure, it’s a scientific theory, a failed one. I’ve personally never noticed any consistent usage by physicists of terms like “theory”, “model” and “hypothesis” in ways that accurately indicate degree of experimental support, don’t see why some writers insist that there is one. I also very strongly object to the article’s standard move of trying to make a failed theory a “mathematical theory”. Mathematics is about well-defined ideas, and there is currently no such mathematical construct as “string theory”. The problems with string theory have nothing do with mathematics, rather have to do with a physical idea that didn’t work out.

To a large extent the problems Conlon is struggling with are ones that the community of string theorists has inflicted on itself. The great majority of writing for the public by string theorists is characterized by large amounts of outrageous hype. For a very recent example, see Daniel Harlow here, who seems to think string theory is a huge success at explaining the standard model

although it hasn’t quite managed to reproduce the complete standard model of particle physics, it comes very close and the obstructions seem more or less technical. I want to emphasize that postdictions are just as good formally as predictions for testing a theory; the distinction is purely sociological.

and that it is also much more (did you know that string theory is what explains the existence of black holes?)

the main reason to work on (or be inspired by) string theory from a scientific point of view is that it may provide explanations of phenomenon that have ALREADY been observed: the existence of black holes, the small positive cosmological constant, and the evidence for an inflationary phase of the early universe.

As for the problem with the multiverse making no predictions, that’s just wrong. We just don’t know what the theory is, when we figure it out, surely it will make predictions:

the issue is not that it doesn’t make predictions. The issue is instead that we do not yet understand it well enough theoretically to know what the predictions are!

I’ve always found reading this kind of thing quite puzzling. My impression of most string theorists is that they’re smart and rather sensible, well aware of the difference between ridiculous hype and an actual scientific argument. Unfortunately such sensible string theorists also have seen no point in trying to write for the public until now, and I’m glad that Conlon’s book finally changes that.

If you followed the reports from the recent Munich conference, you likely heard that the assembled philosophers and physicists nearly unanimously found the anthropic multiverse point of view Harlow advertises to not be legitimate science. Conlon expresses his opinion in this way, and I think it’s the majority one among string theorists, whatever you might have heard:

The most serious problem with the anthropic landscape is that it provides a cheap and lazy explanation that does not come from hard calculation and also has no clear experimental test. It sounds exciting, but does not offer lasting sustenance, and may even act as a deterrent against necessary hard work developing new calculational tools.
Of course, this does no mean that the anthropic approach is necessarily wrong. However the triumph of science has been not because it contains ideas that are not necessarily wrong, but because it contains ideas that are, in some important sense, known to be true: ideas which have either passed experimental test or are glued together by calculation. The anthropic landscape is neither of these. It represents incontinence of speculation joined to constipation of experiment.

Instead of Harlow’s claims that string theory makes lots of postdictions, coming very close to reproducing the complete standard model, modulo some technical issues, Conlon deals with the situation in a much more honest and straightforward fashion. Of the fourteen chapters of the book, chapter 7 is entitled “Direct Experimental Evidence for String Theory.” Here’s the entire content of chapter 7:

There is no direct experimental evidence for string theory.

Conlon’s point of view is different than that of the majority of string theorists in one way, which he explains in detail.

My interest in string theory is in what it can offer to physics that can be probed by experiment.
This view is far from universal. It may seem odd, but most of those who work on string theory are essentially uninterested in any connections with experiment, any public claims that they may make to the contrary notwithstanding.

He backs this up by the observation that less than 10% of talks at recents Strings 20XX conferences have any connection to observable physics.

Here, I’m again in the majority, with his colleagues, who I think have made an accurate evaluation that connecting current string theory to experiment is a failed and hopeless project (I differ with them on prospects for this changing). Conlon has a research program to investigate potentially observable effects of moduli fields, something his colleagues are skeptical about. While I’m also skeptical about this, it does seem like a reasonable thing to investigate, especially since such things may be generic to all theories with extra dimensions, not just string theory. The chapter of the book describing this research is one with material you won’t find in other popular books.

Many of his colleagues have adopted the attitude that, while connecting string theory to experiment is hopeless, it deserves investigation purely as an idea about quantum gravity. While Conlon devotes a fair amount of space to the arguments about quantum gravity and string theory claims about them (including some criticism of loop quantum gravity) he avoids much of the usual hype, and also makes it clear that he himself isn’t interested in pursuing this because of the lack of any hope of ever testing one’s ideas. In some sense I think he and I agree here: it is only if one’s idea for quantizing space-time degree of freedom connects up somehow to our successful theories of other quantized degrees of freedom that one will have any hope of ever knowing whether one has the right theory of quantum gravity. Absent a connection of this kind, one is doomed to become just another cog in an endless fruitless ideological argument about whose quantum theory of gravity is better (or at least, whose sucks less).

Conlon claims that at this point, most string theorists are interested in string theory not as a theory of quantum gravity, but because of applications of ideas that have emerged from string theory to other fields (e.g. AdS/CFT). Here he gives a reasonable account of attempts to use AdS/CFT to say something about condensed matter physics. One place in the book where he, unusually, descends to conventional incantations of hype is his account of applications of AdS/CFT to heavy-ion physics, where he says nothing about the fact that this doesn’t work very well, just repeating some rather stale hype.

There’s a lot else to like in the book, for instance a chapter of highly perceptive descriptions of the different kinds of theorists and the different ways they work, including some rather amusing and mostly friendly caricatures of common behavior. For an example of the kind of thing you’ll read here but not in any other popular string theory book, he notes that certain persons have recently received multi-million dollar prizes based upon model-building ideas that didn’t work out.

There’s a lot more in the book than I have time to discuss, some of which I agree with, some of which I don’t. Obviously I have a different point of view than Conlon’s, but his at least I find to be one with serious arguments behind it, unlike all too much of the popular string theory literature. One thing I found rather discouraging after my book came out ten years or so ago was what seemed to me a lack any serious response from sensible string theorists. Quite a few years later, it’s great to see that Conlon has written such a thing, and I recommend it highly to anyone who cares about these issues.

And, Happy Holidays!

: Sabine Hossenfelder has a posting with a similar take on the Siegel piece. I also like her description of the Munich workshop:

There was, however, not much feud at the workshop, because it was mainly populated by string theory proponents and multiverse opponents, who nodded to each other’s talks. The main feud, as always, will be carried out in the blogosphere…

I haven’t seen the full piece, but New Scientist now seems to be covering the multiverse as theology, which is about right.

Update: Over on Facebook Dan Harlow explains the “technological problems not relevant for questions of principle” needed to get string theory predictions

the idea is that in order to view string theory as a theory of nature, we need to view it as providing a unique probability measure on the space of low energy theories. This would be computed by understanding both the structure of the landscape and the dynamics of eternal inflation. We can then compare our observations to the predictions of this measure, and if they are atypical the theory is ruled out. We are far from doing this though, except for the imprecise cartoon that seems to more or less work for the cosmological constant. This seems just as scientific to me as quantum mechanics, except that we don’t yet know how to compute the probabilities.

I see a bunch of problems of principle here, starting with not knowing the underlying non-perturbative theory and going on from there. Some commenters over there think “It’s hard to even begin to imagine how one can even take Woit seriously.”, but it looks like they take seriously Harlow’s claims that this “seems just as scientific to me as quantum mechanics”, with the minor difference that you can’t calculate anything.

This entry was posted in Book Reviews. Bookmark the permalink.

43 Responses to Why String Theory?

  1. Bee says:

    I preordered the book, but it hasn’t yet been shipped. Looking forward to reading it.

    As to experimental evidence. This isn’t an issue specific to string theory. Actually I think that string theorists are more interested in phenomenology than those working on other approaches to quantum gravity, where (aside from lip confessions) the interest is a grand total of zero.

    My point of view has always been that quantum gravity isn’t science as long as one doesn’t at least try to find experimental evidence. The only other thing worth doing is to prove that one particular theory is the only possible one given certain assumptions, and there doesn’t seem to be much effort devoted to this either. (And why would they? We’d end up in a situation where we would argue about which assumptions are the right ones.)

    Why are there so few people working on finding experimental evidence for quantum gravity? I can tell you it’s not for lack of interest, at least not among the young people, it’s for lack of funding. I get a lot of requests from students and postdocs who want to work with me, but I have to turn then away because I have no funding. I barely managed to get funding for my own research (kudos to FQXi). And lest you think it’s because I am just a mediocre scientist, let me add the following twist.

    At some point I concluded that quantum gravity phenomenology is a bad, bad field to work on because it flops through peer review, which is almost certainly conducted by people who in the majority think that funding should go into further mathematical speculations. Seeing that my colleagues who work on AdS/CFT have funds thrown after them, I applied for funding in that field too. Nevermind that I have basically zero prior experience and the field is entirely overpopulated already. I got on first try funding for two postdocs positions (or actually for my own position, a complication that I still have to sort out).

    Then I have to listen to certain Nobelprize winners who insist that the reason scientists work preferably in one field and not another has nothing to do with funding, which eventually is allocated by peer opinion, leading to a rich-get-richer trend. No, scientists are totally unaffected by this and only follow their personal interests, in a completely objective and unbiased manner. So now I work on AdS/CFT (or rather, my postdocs do). Completely unbiased by funding opportunities.

    The problem is that the people at top institutions, the ones with the big names and the many awards and the big prizes, are the ones who we read about in the press. And they have by and large pretty much no contact to the reality of research life.

    Why don’t journalists for a change call up some dozen string theory postdocs and ask them how they came to work on what they work on and why they work on what they work on? I have asked this question to a lot of postdocs over the years and I can tell you what the replies would most likely be. “I read Brian Greene’s book,” is a reply I got to hear a lot. But besides this it is mostly “I wanted to work on quantum gravity and string theory was the only option.” And most young students don’t realize that they are very likely to get stuck on the topic of their PhD thesis, unless they switch fields very quickly afterwards. And so it happens. These are the stories the public does not get to hear about.

    Sorry for the rant, I find it all very frustrating, seeing that so little has changed in the last ten years. And happy holidays to you too 🙂

  2. Giotis says:

    I don’t see a contradiction or a distinction here.

    By now it is more than clear, even to its critics I believe, that String theory and the generic Stringy framework with all of its tools is more than relevant for Nature; it has been proven again and again that it can be used to help us answer some (if not all) of the deepest questions about the fundamental nature of reality and in the process it raises new ones which is equally important.

    The theory is at the center of a web of deep ideas binding them together; but the picture is far from being complete or clear; in that respect people have no choice but to follow the theory and see where it leads. To do so they must explore all of its streets and highways and this is what people do I guess; phenomenology is one aspect of this endeavor.

  3. Warren says:

    One thing even string people seem to forget is the reason string theory got started in the first place was the experimental fact that both the spectrum and small-angle scattering of hadrons follows linear Regge trajectories that are predicted only by string theory. The facts that the known string theories predicted the wrong intercepts and spacetime dimension turned phenomenologists off to this approach.

  4. Jesper says:

    @ Bee, I would suggest that one reason why Quantum Gravity phenomenology is not very popular to work on might be the obvious one that we don’t yet have a credible theory of quantum gravity that produces predictions – and without that we don’t know what experimental evidence to look for. Am I wrong?

    In all this debate about quantum gravity, experimental evidence and whether we should change the notion of science I would say that a credible test of a ‘final theory’ is that it should essentially postdict the entire standard model – or at least most of its essential structure such as number of generations, gauge groups etc. Nothing less. And until we have that – and the wait might be infinite – then the question of a final theory should simply be left as ‘undecided’.

    Also, I can report that the “No, scientists are totally unaffected by this and only follow their personal interests,…” is not correct. I think that we all have a responsibility and obligation not to give in to the funding pressure and insist on following our own interest – essentially at all cost. Because if we don’t we become corrupt, we become part of the problem.

    Of course the system sucks – but systems often do! And nothing can prevent someone from just doing whatever he/she wants if he/she insists – there are other ways to fund research than through research grants and university positions.

  5. Peter Woit says:

    Thanks for the comments. The AdS/CFT phenomenon is quite remarkable and deserving of its own book. I see that the Maldacena paper is up above 10,000 citations, way off scale anything that has ever happened in the history of physics. What I’ve heard time and again from young theorists is that they go into AdS/CFT because it’s something that seems to be not understood, seems to be both a new deep idea about quantum gravity, and to have other applications, and, of course, it’s where most of the jobs are. The coverage of AdS/CFT in Conlon’s book reflects this, with hype level a bit less than the usual, still somewhat uncritical to my taste. An accurate take on this story awaits another book, one by someone who has mastered some fraction of those 10,000 papers and is able to cut through the hype and seriously evaluate what is known, what isn’t, what works and what doesn’t. Unfortunately I don’t think we’ll see this soon.

  6. Peter Woit says:

    Some things about the Conlon book I didn’t mention is that he’s rather skeptical about how successful AdS/CFT has been as a technique to study QCD. He writes somewhat wittily:
    “This research, aiming to reproduce the properties of the actual strong force, has now been carried on for over a decade, with more or less degree of rigour and less or more degree of success.”

    One place where I strongly disagree with him is that he argues essentially that it’s not worth working on strongly-coupled QCD, that this is no longer an important frontier problem in physics, so does not deserve to be funded.

  7. Conrad says:

    Bee, Peter,

    quantum gravity is a tough field to work in for two reasons. First of all, people honestly are looking for observable effects. This prevents them from going to far into fantasyland. Secondly, many models predict the lack of such observable effects.

    Even the simple prediction of an observable effect would make a researcher famous. But no prediction has ever been formulated that stood up to the test of the community.

    My personal impression, following the field in the past decade, is that no observable quantum gravity effect exist (except the cosmological constant, of course). Of course, this conclusion is tough to swallow. But if the impression is correct, it is a wise move to change field!

    We can also ask the opposite question: Bee, why are you convinced that other observable quantum gravity effects should exist in nature? There must be some reason(s) for your gut feeling and for your – admirable! – tenacity. Can you try to formulate it?

  8. Shantanu says:

    Peter: Is Conlon a physicist? What does he critic about LQG? Does he say anything about asymptotic safety or CDT?

    Bee, Peter : Yes unfortunately there is a lot of hype about certain trendy fields (ADS/CFT been one ). Another one been is calculating the GW signal from black hole/neutron star binary where gravity division of NSF has thrown in lots of money.
    OTOH no funds for QG phenomenology and also various other interesting topics
    in GR and alternate GR theories. However weren’t institutes like Perimeter institute
    and other such places set up to give freedom to people to work on non-mainstream ideas? It looks like they are also following fad trends.

  9. Bee says:


    The whole point of phenomenological models is that you work them out to test for “new physics” even if you don’t know the complete underlying theory. In quantum gravity, the most common examples are space-time fluctuations (eg decoherence caused by), defects in the structure of space-time (deviations from GR), violations or deformations of Lorentz-symmetry, consequences of the Planck length setting a limit to the resolution of shortest distances, and so on. All these are possible consequences of quantum gravity that can be searched for by help of phenomenological models.

    In particle physics there is a whole industry behind producing phenomenological models that quantify “beyond the standard model physics” so that data can be analyzed for traces of it. We’ve spent the last 3 decades hunting for particles that aren’t there. I think it’s more than time to look for something more promising.

    Incidentally, you are wrong in saying that it “isn’t popular”. It is in fact very popular, which has its own downsides. Every time someone writes a paper that supposedly tests something quantum gravity, it is all over the news. Unfortunately, much of this research is rather shallow and low quality, an issue that would be remedied by better funding.

    And your remark “of course the system sucks” is one of the most common excuses I hear. So common you will find it mentioned on the slides of a recent talk that I gave as the main cause of the problem. There isn’t any “system” other than us.

  10. Bee says:


    My main point is really the following: If you don’t think that quantum gravity has observable consequences, then it isn’t science and no science funding should go into it. If you invest into quantum gravity as research in a scientific discipline, you also must invest into studying its potentially observable effects. Where are the dozens of research groups dedicated to quantum gravity phenomenology?

    As to my “conviction”. In brief I’d like to quote the “principle of finite imagination,” that says just because you can’t imagine something doesn’t mean it’s impossible. Over the history of science, it has happened over and over again that something once deemed impossible became possible. I haven’t come across one single convincing argument that no quantum gravitational effects can be detected. Why are you so convinced that it isn’t possible? And just to be clear, I don’t necessarily mean direct effects.

    To speak of my personal opinion, presently the most promising areas seem to me CMB entanglement and massive quantum oscillators. Both of these only test the perturbative end, but at least that would move quantum gravity into the realm of being an actual science. Imagine how awesome this would be. You’d think that hundreds of people work on this. Instead it’s maybe 10 and I’m being generous on that count.

    The non-perturbative end is of course much more difficult. You would want to look at relics from the early universe, and to solve the inverse problem one would almost certainly have to combine different observables.

    Another possibility are naked singularities. It has been claimed some years ago that naked singularities (contrary to expectation) might actually be created in gravitational collapse without requiring very special initial conditions. This would mean that we potentially could have uncensored view of strong curvature regions. Remains the question how would you tell a naked singularity from a black hole and what could we learn from this?

    You might not agree that these are interesting experiments. But getting an answer for which experimental avenue is the most promising is exactly why this field needs funding.

  11. Jesper says:

    @ Bee

    perhaps we have misunderstood each other slightly. I read your first comment as a complaint about the system, which eventually lead you to apply for funding in a field, which you are not interested in, namely AdS/CFT – and that you are now working there (or your postdocs). My reaction is that I find this a wrong choice of action. I do not like “bread-and-butter” type research, where people do research in order to survive and progress in the system as it is now. There is way too much of that. I think that funding should not play a role when choosing a research subject.

    And I completely agree with you when you write that there is no system except us – and I would love to see more people try to rebel against it.

    To change a system takes sacrifice, it is always easier to work with it. In my own case I have now worked for more than four years without research funding – essentially because I refuse(d) to work on subjects, which might have secured me a career. I don’t see any law of Nature that dictates that you can only do research on university funding.

    As to phenomenology I am certainly no expert. There is of course a difference between BSM physics and quantum gravity phenomenology – and my take on the latter is very much aligned with what Conrad wrote in the above. I suspect that the only observable effect of quantum gravity might be the standard model itself.

  12. Lee Smolin says:

    Dear Bee,

    I agree with your main points but would disagree when you assert that “those working on other approaches to quantum gravity, where (aside from lip confessions) the interest (in phenomenology) is a grand total of zero.” Here is a list of potential quantum gravity phenomena which have been proposed and studied over the years by different people.

    -Lorentz symmetry breaking.
    -Deformation of Poincare invariance.
    -Dispersion by Planck scale discreteness of quantum geometry.
    -CPT violation
    -parity violation connected to lorentz symmetry breaking.
    -parity violation in gravitational wave production by inflation leading to detectable effects in tensor modes.
    -Corrections to Hawking radiation, coming from planck scale geometry, observable in patterns of lines superimposed on thermal Hawking spectrum, potentially observable in bursts coming from evaporating primordial black holes.
    -Planck star models of black holes as sources of fast radio bursts.
    -Effects at low l modifying the CMB spectrum coming from a bounce replacing the initial singularity.
    -Diffusion in momenta of quanta propagating on causal sets.
    -Dimensional reduction, ie modifications in the spectral dimensions of quanta propagating on quantum geometries.
    -Gravitationally induced non-linearities in quantum evolution (Penrose, D’iosi etc).

    Apart from pure quantum gravity phenomenologists, these proposals have come from people studying LQG, spin foam models, causal sets. asymptotic safety, causal dynamical triangulations, emergent gravity. As you know well, because you are an organizer of it, there are enough people working on quantum gravity phenomenology to populate a 80-100 person meeting every year or two.

    I agree that so far no novel phenomena have been observed, but we do have impressive limits on some of these, some of these above the Planck scale.



  13. Gregor says:


    10000 citations is really a lot. But the statement that this is “way off scale anything that has ever happened in the history of physics” is exaggerated. It is well known that the largest fraction of physicists work in the field of condensed matter physics. In this context electronic structure methods are the theoretical workhorse. Therefore it is natural that a search for the most highly cited articles in APS journals mainly reveals articles related to electronic structure theory. These articles are more often cited than Maldacena’s paper. Here is a (very incomplete) list:

    Physical Review 136 (3B) B864; Physical Review 140 (4A), A1133; Physical review letters 77 (18), 3865; Physical Review B 45 (23), 13244; Physical Review B 23 (10), 5048; Physical Review B 46 (11), 6671; Physical Review B 41 (11), 7892; Physical Review B 59 (3), 1758; Physical Review B 13 (12) 5188; Physical Review B 54 (16) 11169

    Of course, this only tells us that there are more people working in this other subfield of physics or, perhaps, that the citation manners are different in these two areas. If Maldacena’s paper is a basis for the usage of certain mathematical structures in different areas of physics then an explanation for the high citation numbers might be that it is interesting for a much larger crowd of physicists than only the string theory community.

  14. 4gravitons says:

    Interpreting Harlow’s post as arguing that the standard model is a postdiction of string theory seems fairly disingenuous, as the clarifications that he added to the post should show. String theory does get quite close to reproducing the standard model, and the obstructions there do indeed appear to be technical. That doesn’t mean it uniquely reproduces the standard model as the only possible stable state, or even that the standard model is the most likely such state, just that the standard model appears to be one possible configuration. Meanwhile, as Harlow clarifies, the “postdictions” he’s referring to are things like the existence of gravity, not the standard model.

  15. Neil says:

    “It represents incontinence of speculation joined to constipation of experiment.”

    Very quotable.

  16. Peter Woit says:

    Conlon is a well-known young string theorist. His criticism of LQG is fairly long and I can’t reproduce it here (and am not interested in engaging in that particular argument). I don’t recall anything about asymptotic safety or CDT, and as I noted I don’t think Conlon is fundamentally that interested in the quantum gravity issues, for reasons he explains.

    What Harlow is referring to by “it comes very close [to completely reproducing the standard model] and the obstructions seem more or less technical.” are arguments that you can get essentially any low energy physics out of “string vacua”. I think he’s found the most misleading way possible of saying that string theory is a completely empty idea as far as particle physics goes. Any one who wants to can read what Harlow wrote, read what I wrote, and decide who it is who is being disingenuous here. The added material you mention is mainly his response to Scott Aaronson’s pointing out to him that his claim of no real distinction between postdictions and predictions is nonsense.

    I did go take another look at the Facebook posting, noticed that after writing that long piece of hype, Harlow’s attitude is that he’s now too busy doing serious science to respond to any criticism of it. I would like to see him respond to Conlon, who explains clearly what the problem with Harlow’s claims about the multiverse are.

    I also see that writing a posting mainly saying nice things about a book defending string theory and wishing everyone happy holidays draws comments from string theory ideologues about what an embittered person I am….

  17. Peter Woit says:

    Please, if it’s not about the Conlon book or the Siegel or Harlow pieces, please resist the temptation to submit comments, especially those about how you feel about quantum gravity…

  18. Bee says:


    Yes, I think you misunderstood this, sorry. I am still working on qg pheno. But I am feeling rather stupid about it to be honest. Not because I think it’s not a good research area, but because I am willingly sabotaging my future prospects of continuing to work in academia at all. (Actually, I wanted to leave, but then the money came through. So now I have two years to figure out what to do next.)

    Your idea that scientists ‘should not’ be affected by funding opportunities is just totally past reality. People go where money goes. Show me any reason why I should believe this isn’t so in science.

    The people who ‘rebel’ against the system are the ones who are forced to leave. That’s reality. Consequently the ones who stay are the ones who are, by and large, fine with what’s happening because they themselves benefit from it.

  19. Bee says:

    Dear Lee,

    There are enough people to populate an 80-100 person meeting, yes. The next one of which, incidentally, is due next year and doesn’t have any funding whatsoever. As I said above, it’s not that there is no interest in the topic. This isn’t the problem, especially not among the young people. The problem is that there’s no funding and no positions.

    The vast majority of people working on these topics do it as an occasional on-the-side paper because it’s not research that one can actually live from.

    How many people can you list who have a position that pays full time for qg pheno? I could come up with maybe ten. How many positions have there been in the last decade searching for candidates in qg pheno? I know of maybe three. How many research groups on qg pheno are there in the world? Two? How many positions have there been for LQG and string theory in comparison? How many departments have string theory or LQG groups, or the occasional other theoretical (mathematical?) approach to quantum gravity. Right. Do you really believe that this is a good balance between theory development and phenomenology?



  20. Low Math, Meekly Interacting says:

    I didn’t think Siegel’s piece was so bad. A bit extremist perhaps, but maybe more people need to stick their necks out a little and advocate for staunchly conservative point of view, even if it’s a bit mythical. I’ll take that over “post-empirical science” any day. I’ve said more-or-less the same thing before, but in just about every other branch field of physics (or any other branch of science, for that matter), there’s no need for these philosophical debates. Contact with experiment is taken for granted, and difficulties that are generally down to instrument sensitivity or funding. If quantum gravity and unification research could be sufficiently compartmentalized, I doubt anyone but a few esoterists would care about the debate, such as it is. But it can’t be compartmentalized. Many scientists from all disciplines and millions of non-scientists alike idolize people like Einstein and Hawking. It’s human nature to be fascinated, even spiritually moved, by the search for an “ultimate theory”. So when the very people who are perceived as holding this knowledge go around re-defining science to fit a “post-empirical” paradigm, the effect is disproportionately influential on public perception, and, in my opinion, highly damaging. Maybe Siegel missed some nuances. There’s so much nuance in the discussion already veritable geniuses can’t agree on the most basic level about what “science” is anymore. I’ll take Siegel’s perspective over that alternative any day.

  21. Jesper says:

    @ Bee

    “Your idea that scientists ‘should not’ be affected by funding opportunities is just totally past reality. People go where money goes. Show me any reason why I should believe this isn’t so in science.

    The people who ‘rebel’ against the system are the ones who are forced to leave. That’s reality. Consequently the ones who stay are the ones who are, by and large, fine with what’s happening because they themselves benefit from it.”

    I actually agree with you – but I don’t think it has to be that way and I don’t agree that people, who are forced to leave, have to stop doing research. Why is it a black and white picture, where either you are ‘in’ and doing research or you are ‘out’ and not doing it?

    Imagine if you applied the same logic to artists – do artists stop producing art when they have no money? No, of course not, they eat porridge for a while, live on the dole, find a patron, whatever. I think that science and art are related in this respect, its a question of passion, idealism –

    – the only example I can give you (but I’m sure there are others) is myself. I was forced to leave some years ago – my research is way off mainstream, but I publish in top journals – and I have continued my work and have manage to get funding elsewhere.

    I see very little reason to stop doing what I love just because the flow of cash stops – I just have to adjust and push on, and I’ll do that as long as I believe in what I do. This is the type of rebellion I would wish to see more of. If the funding system sucks, well, then find your money elsewhere! If you really believe in what you do, then you’ll find a way – I don’t agree that being a scientist is a profession – to me its a lifestyle, a passion, a vocation.

  22. Shantanu says:

    Jesper : if you don’t mind, could you list the sources from where you get funding, since I am sure that would be of interest to many people. FWIW, I know another person,
    who had a hard time getting a job (or invitations for conferences/seminars) for about 8 years, but still published papers in top quality journals by working in evenings and weekends and taking a day job in biophysics to pay bills. eventually he did get a job in a teaching university with time available for research. But I agree with Bee that probably such cases are almost non-existent. Maybe you and him are the only current examples.

    Lee : once upon a time PI had an option where anyone could propose to organize conferences as long as the LOC/SOC involved one PI resident faculty and it would provide logistic support. Is such a service no longer available? At any rate I do hope that PI would organize the next incarnation of the QG phenomenology conference to keep the tradition.

  23. Jesper says:

    @ Shantanu,

    I know that there are very few examples of people who work without research funding. My point is that I don’t see why it need to be that way. An example: Schwarzschild did his important work while fighting in WWI. History is full of people who didn’t stop just because conditions were a little (or very) challenging. But it appears that today people just stop when they don’t get paid to do research. This I don’t really understand. I think that the analogy with artists is relevant.

    As to your question: I don’t want to expose my private finances here, I can just say that at the moment I finance my research out of my own pocket.

    Perhaps one can turn the question around: isn’t it conceivable that one can get better research conditions outside the universities, where so much time is now taken up with things that has nothing to do with research?

  24. Peter Woit says:

    This has gotten completely off-topic. Whatever the prospects are for financing one’s research oneself (easy for some people, impossible for many others), efforts like Sabine’s to hold the current system to account are extremely important. Conlon’s book discusses funding issues extensively, and his efforts, like those of Harlow, have a lot to do with fighting to preserve funding for string theory in the face of bad PR like Siegel’s article. None of them are planning on giving up this fight in favor of doing string theory in their spare time.

  25. 4gravitons says:


    I do appreciate your perspective on Conlon’s book, but I wasn’t intending to gloat about it. 😉

    (More seriously, I suspect you’ll see more pieces like that as time goes on. Science communication seems to work by establishing tropes and building on them, and the sort of tropes Conlon is working with are a newer invention, the result of a younger string theory community finding its voice.)

    I just think you’re being more than a little unfair to Harlow. Yes, he’s using older tropes…but in the context of a (non-Sean-Carroll) facebook post. Most of his expected audience understands what he’s referring to, or at least are people like Scott Aaronson who are likely to ask for clarification. I doubt Harlow expected his post to go viral.

  26. Peter Woit says:


    I don’t see Harlow as using older tropes, but actually newer ones, albeit highly extremist ones. Does anyone not trained at Stanford believe claims like his that the reason we don’t currently have testable statistical string landscape predictions is “a purely practical problem, not one of principle”? I don’t think there’s any way to construe that statement as anything other than a piece of outrageous hype. Sure, if you wanted to, you could find some way of construing some of his other statements so that they weren’t obvious nonsense (e.g. by making his “postdictions” claim not apply to the SM, although he makes it in that context and doesn’t explicitly say it doesn’t apply there). I think he honestly believes what he’s saying, but I also think most physicists recognize it as not science, and if voices like his dominate those like Conlon’s, you’re going to see a lot more, accurate, “String theory is not science” articles in the future.

    One amusing thing about his post. According to his definition, everything I teach and think about all day is “string theory”. I hadn’t realized that….

  27. Gil Kalai says:

    I liked Harlow’s piece. It is clear and short and it makes quite a few interesting points some of which are new for me. I liked especially the following points:

    “3) Just because string theory reproduces known physics, that of course doesn’t mean that we should declare victory for it. But it does mean that we should take it seriously. In particular one should note that none of its “competitors” have done this.

    4) Except for one: the effective field theory of the standard model coupled perturbatively to general relativity (EFT for short). This theory also accounts for almost everything we have observed (except dark matter, neutrino masses, perhaps inflation). EFT is the real nemesis of string theory: what would convince us to prefer string theory to it?

    5) I would say that there are two basic reasons by which we can prefer one physical theory to another. One is of course if one theory correctly accounts for observed phenomenon that the other doesn’t. The other is if one theory explains the same observations using fewer parameters.

    6) As far as we can tell, string theory may eventually beat EFT on both of these criteria…”

    So Daniel’s point is that (at present) the main scientific alternative (“nemesis”) of string theory is not the even more speculative and much more partial suggestions for quantum gravity (the “competitors” as Daniel referred to them), but a rather straightforward coupling (EFT) of the standard model with general relativity. (I suppose that like string theory also EFT should not be thought as a single possibility but is quite board. Perhaps not quite as board as ST itself.)

    Daniel expects (or hopes) that eventually some variants of ST will beat all variants of EFT (which is a perfectly fine), and, taking for granted the ST framework (which is also perfectly fine), he even regards some major remaining difficulties as of “technological” nature irrelevant to “matters of principle.”

    There were other interesting points (like the value of postdictions, the distinction between practical matters and “matters of principle” and a few more ) in this piece, so I was quite happy to read it.

    Regarding the issue of “science”. Since I regard mathematics as science the debate regarding this term is little moot for me (interesting questions arising from philosophy of science notwithstanding.)

  28. Peter Woit says:

    Gil Kalai,

    Saying “string theory reproduces known physics” is extremely misleading, when what you mean is that it can reproduce not just known physics, but basically anything. As for the idea that string theory reproduces the standard model with less parameters, that’s simply untrue. If he wants to hope that string theory will beat EFT on these criteria, he’s welcome to do so, but, after 30 years, there’s zero evidence of this working. There’s a fundamental problem with the way he and other string ideologs argue, which is basically: “First, assume everything we would like to be true is true, then…” As for the claim that the problems are just “technological”, not “matters of principle”, I think that is not just hype, but absurd hype.

  29. vmarko says:

    Regarding the “technological problems” of ST, it would be really good if people would remember the extremely sarcastic way in which Pauli was mocking some of Heisenberg’s similar statements, a century ago. Namely, he took an empty canvas, put it in a frame, and said “This proves that I am as good a painter as Titian. Only some technical details are missing.”

    Also, I often hear the off-the-cuff statement that general relativity can be combined with the Standard Model in an EFT. This isn’t really true — one can only combine them classically, i.e. take the classical limit of the SM and plug it into Einstein’s equations. There is no such thing as an “effective quantum theory of gravity”, be it GR+SM or otherwise. Looking at low-energy behavior (i.e. putting a cutoff at some scale) isn’t enough — one needs to define the path-integral measure for the effective gravitational degrees of freedom (if one is to have a quantum theory at all), and this is an unsolved problem even in the context of EFT.

    This is in contrast to the SM in flat spacetime, which certainly can be regarded as a low-energy EFT of some more fundamental theory. The measure is there, the dof’s are known, everything is well-defined. But for gravity none of this works, because we don’t know what are the dof’s, and because of measure issues — and this *despite* the presence of a cutoff.

    So I’d say that neither ST nor EFT can describe all observed experiments. ST has trouble with the matter sector, EFT has trouble with the gravitational sector. Lose-lose.

    Best, 🙂

  30. Anonyrat says:

    What is the experimental result or observation that EFT has trouble with?
    Thanks in advance!

  31. vmarko says:


    The trouble with EFT is not experimental, but theoretical: there is no theory! Nobody is able to write down the equations for an effective low-energy quantum theory of gravity. The measure of the gravitational path integral is not well-defined, so the theory does not exist, let alone experimental predictions. This was known back in the ’60s and ’70s, when DeWitt was studying the measure for the gravitational path integral. Already then it was obvious (to the well-informed) that any discussion of QG requires one to formulate a UV completion, precisely because an effective field theory doesn’t exist. If a QG EFT were possible, by now people would have long forgot about strings, LQG and other Planck-scale theories, and be content with an effective low-energy theory.

    Best, 🙂

  32. Peter Woit says:

    Sorry, but I have to keep pointing out that this is not a quantum gravity discussion board. If people want to discuss Marko’s comment with him, please contact him directly.

  33. amused says:

    Since Conlon apparently discusses sociological aspects, did he explain why, in competition for jobs in particle theory, N single-author publications in Phys.Rev.Lett. by a non-string researcher (N being any number between 1 and infinity) count for flat zero when weighed against just one article in, say, PRD by a string researcher where he/she was one of eight authors on the paper with the others all being more senior people?

  34. Peter Woit says:

    No mention of that…
    More generally, I didn’t notice much awareness of the problem of faddishness, of pressure to work on certain designated “hot” topics if one wants a career in the business.

  35. srp says:

    I just read Maguejio’s 2003 book on VSL (found it used). Minus his profanity and ageism, the same points about U.S. theorists all working on the same trendy stuff and getting funded only for doing it is in there. It would be nice to see some systematic evidence about this funding issue.

  36. Peter Woit says:

    Quantifying the grant issue in the US would be a bit tricky, for one thing many grants are to groups. As many US HEP theorists will tell you, grant amounts have been going down, as far as I know, independently of area people work in. It would be interesting though if anyone has any data.

    One somewhat more promising way to quantify faddishness and which fields are hot would be to look at the postdoc hiring data here
    You’d have to figure out how to categorize people’s research fields, which would not be so easy.

    In Conlon’s book, one thing he emphasizes is that he has had to convince committees of non-string theorists to give him a grant (and has been successful). He emphasizes quite a lot that connection to experimental testability is an important part of his work, and seems well aware that that argument is now an important one to be able to make if you’re a string theorist and want a positive evaluation from other physicists. That may not actually be a good thing, if you believe that the current state of string theory cannot successfully make contact with experiment, that the best hope for the future is more formal work that would uncover something new about the underlying theory, something with a better chance at connecting to experiment.

  37. Scott Church says:

    Peter or Anyone,

    Regarding grant requests and/or postdoc hiring for string theory research emphasizing “[connections] to experimental testability,” how many of these proposals are based on postdictions rather than predictions? Can such proposals be taken as a sign that things are trending away from Texas sharpshooting, or what might be called the Kane Effect? If so, how many of these proposals seem to show real promise?

  38. Peter Woit says:

    Scott Church,
    I think most people hoping to get a “test of string theory” are looking for predictions, would be happy though to get a postdiction, and this hasn’t changed. As I’ve documented extensively on this blog, the story of “tests” of string theory is that they’re never tests that can falsify string theory. They refer to some possible observable effect in some model, a model supposed to have something to do with string theory (sometimes just “string-inspired”). The problem is that if such an effect is not observed, that just means you change to a different model. Kane’s “predictions” are of this kind, and Conlon’s work on observable effects of moduli is also of this kind (Kane is different in the way he markets such “predictions”, in the much stronger claims for them he makes). I don’t think any of these show significant promise, since the models being invoked don’t actually plausibly explain anything we know about.

    Conlon I think does explain this fairly clearly. The motivation of his search for models with observable effects of moduli is not that string theory implies such specific models are likely. It’s more that string theory provides the inspiration for looking at such classes of models, which give new ideas for unexpected things to look for. While such things are unlikely to show up, if one did see them, they would indicate dramatic new physics of some kind.

  39. life of brian says:

    [Low Math Meekly “Interacting] I didn’t think Siegel’s piece was so bad…[]…maybe more people need to stick their necks out a little and advocate for staunchly conservative point of view”

    It’s certainly one possibility…that Siegel has taken a courageous stance for deeply held principle. Another possibility is the severe to terminal String Theory critique in media has lately begun to fizz.
    Finger in the wind or principled and potentially self-sacrificial harsh criticism? In the end you’d have to decide what else you’d expect to see given one, or the other respectively.
    Evidence of serious long term consideration perhaps. One way to get an indication on that might be to ask what are the hackneyed positions out there. If the space is starting to fizz, then chances are the ill thought through, pointless or point-missing, components of criticism are the ones becoming commonplace so hackneyed, so the ones showing up disproportionately right now. How’s he doing so far?

  40. Peter Woit says:

    life of brian,
    More or less identical arguments over string theory have now been going on for a decade or so, without a lot of change. The only thing that I see having changed in the last couple years is that the LHC results are shutting off the last hope for some observable new physics relevant to string theory (pre-LHC a common argument argument from string theorists was that connection to experiment would be made through the discovery of SUSY at LHC energies).

    The naive “it predicts nothing observable so it’s not science” critique of string theory is now more powerful than it used to be, as more and more string theorists adopt the attitude that nothing observable is not a problem for the theory, attracting a reaction like that of Ellis/Silk. My impression is that Siegel is well-aware of some of the subtleties of the arguments over string theory, also aware of the fact that the naive critique has gained force from recent developments, so he thought it was worth making now (popular science articles in Forbes aren’t a place you can really do subtlety).

  41. Pingback: The Sense of Scientific Style | Skeptical Swedish Scientists

  42. Greg says:


    is string theory probable at all? I ask for the following (humorous) reason. A supersymmetric theory has about 105 free parameters. Each parameter can have at least 10 million possible values (a rough guess). That makes 10^735 possible parameter combinations. But the landscape/multiverse has only 10^500 options. I would deduce that there is only a probability of 10^-235 that standard model plus gravity is part of the landscape.

    What is wrong with the reasoning? 🙂 Happy holidays to you too!

  43. Ignatz Ratzkywatzky says:

    Going through John Baez’s Crackpot Index, I note that the last and highest scoring item is #37:

    “50 points for claiming you have a revolutionary theory but giving no concrete testable predictions.”


Comments are closed.