First in a prospective series of my own versions of the best arguments for conclusions I don’t personally share. I’m supposed to stick to statements that I believe are true, even if I don’t think they warrant the conclusion. The idea is to probe presuppositions, put our ideas to the test, and of course to implicitly diss the less-good arguments for things we don’t believe. And who knows, maybe we’ll come up with arguments that are so great we’ll change our minds! (By slipping into the royal “we” I’m encouraging others to play along.) So here we go: the best argument I can think of for why research on string theory is a waste of time.
Traditionally, the greatest progress in physics has come through an intense interaction between theory and experiment. We have learned new things when experiments were good enough to bring us data that didn’t fit into the models of the time, but our theoretical understanding was also sufficiently developed that we had the tools to formulate useful hypotheses. While we know that classical general relativity and quantum mechanics are fundamentally incompatible and must someday be reconciled, straightforward dimensional analysis suggests that detailed experimental information about the workings of such a reconciliation (as opposed to true-but-vague statements like “gravity exists” or “spacetime is four-dimensional on large scales”) won’t be available at energies below the Planck scale, which is hopelessly out of reach at the current time.
A defensible response to this lack of detailed experimental input would be to place the problem of quantizing gravity on the back burner while we think about other things. And this was indeed the strategy pursued by the overwhelming majority of theoretical physicists, up until the 80’s. Two things caused a change: the drying-up of the river of experimental surprises that had previously kept particle theory vibrant and unpredictable, and the appearance of string theory as a miraculously promising theory of quantum gravity. Even though the Planck scale was still just as inaccessible, string theory was so good that it became reasonable to hope that we could figure it all out just by using brainpower, even without Planckian accelerators.
But it hasn’t worked out that way. Gadflies point to the landscape of low-energy manifestations of string theory as the nail in the coffin for any hopes to uniquely predict new particle physics from string theory. But that is only a subset of the more significant challenge, and understanding particle physics beyond the Standard Model was never the primary motivation of most string theorists anyway — it was quantizing gravity.
The real problem is that string theory isn’t a theory. It’s just part of a theory, and we don’t know what that theory is, although sometimes we call it M-theory. As Aaron explains in a very nice post, the thing we understand is “perturbative” string theory, which is a fancy way of saying “the part of M-theory where small perturbations around empty space act like weakly-interacting strings.” We’ve known all along that colorful stories about loops of string propagating through spacetime only captured part of the story, but we’re beginning to catch on to how difficult it will be to capture the whole thing. The Second String Revolution in the 90’s taught us a great deal about M-theory, but it’s hard to know whether we should be more impressed with what we’ve been able to learn even without experimental input, or more daunted by the task of finishing the job.
Within our current understanding of string theory, there is not a single experiment we can even imagine doing (much less actually, realistically hope to do) that would falsify string theory. We can’t make a single unambiguous prediction, even in principle. I used to think that string theory predicted certain “stringy” behavior of scattering cross-sections at energies near the Planck scale; but that’s not right, only perturbative string theory predicts such a thing. “String theory” is part of a larger structure that we don’t understand nearly well enough to make contact with the real world as yet, and it’s completely possible that another century or two of hard thinking won’t get us to that goal. It made sense to be optimistic in the 80’s that there was enough rigidity and uniqueness in the theory that we would be led more or less directly to contact with observation; but that’s not what has happened.
The best reason to think that research on string theory is largely a waste of time is because it’s just too hard.
Pretty convincing, eh? But I don’t buy it, even though I think I’ve adhered to my self-imposed rule that I believe every individual sentence above. It might turn out to be the case that another century or two of hard thinking won’t get us any closer to connecting string theory with the real world, but I don’t see any reason to be that pessimistic. The thing that’s really hard to get across at a popular level is that the theory really is rigid and unique, deep down; it’s the connections between “deep down” and the world around us that are the hard part. Count me as one of those who is more impressed with what we have learned than daunted by what we haven’t; if I were to bet, I would say that more thinking will continue to lead to more breakthroughs, and ultimately a version of M-theory that can rightly be called “realistic.”
In the meantime, the advent of sexy new data from the LHC and elsewhere will draw a certain fraction of brainpower away from string theory and into phenomenology, but there will be plenty left over. The field as a whole will fitfully establish a portfolio of different approaches, as it usually does. And there will undoubtedly be surprises around the corner.
the Ancient Philosophers used to sit on a stone all day and think and think and think and they came up with very beautiful and elegant theories which were all wiped out in the Age of Empiricism.
Research on String Theory is a Largely Waste of Time
Because it simply isn’t necessary.
I think it is now settled that string theory is not a theory of everything and it still aspires to be a theory of something. Research done with that firmly kept in mind is quite OK by me. What was wrong prior to Smolin, Woit et al was the constant insistence that string theory as it currently is applies to reality. It is rather different from the (perhaps well-founded) hope that string theory will one day be connected to reality.
So instead of arguing, let me ask – what are the most bizarre 4-large 6-compactified dimension worlds that can appear in the landscape? This requires a definition of “bizarre” I guess, but perhaps that too is a subject for discovery. The underlying purpose would be to see one can come up with a guess as to a physical principle that ought to exist in order to rule out such worlds.
” Research on String Theory is a Largely Waste of Time ”
That’s going to annoy me for the rest of the week… Fix it!
Arun,
I think it’s more correct to say that string theory gives us pieces of the theory of everything. All of the pieces have yet to be put together and some remain unknown.
Arun,
I think it’s more correct to say that string theory gives us pieces of the theory of everything. We have yet to put all of the pieces together and yet more pieces which are currently unknown may be required.
string theory gives us pieces of the theory of everything
hahaha… prove it.
I do not know whether string theory is the right approach to understanding reality at its smallest, and for reconciling particle physics with the theory of relativity. However, there is no doubt that we will figure this out for the simple and compelling reason that we are hard wired to do so. In a novel I wrote I have the major character makes this point through the aphorism that, “Life knows life.”
It’s probably been made before, but here’s an outsider’s suggestion: Proclaim string theory (or hypothesizing or whatever) a branch of mathematics. Poof – problem solved. No worries about legitimacy embarrass mathematicians just because their fascinations have no practical ap (yet). I’m a little shaky on history, but wasn’t Riemannian geometry, among other non-Euclidian geometries, a perfectly respectable line of exploration over at the Math Dept. before Einstein and other relativity pioneers used it to practical effect? And there’s no reason a physicist shouldn’t hone his or her math synapses by looking into pure-math fields — esp. those that seem, even hazily, resonant with the universe’s behavior.
Sorry Sean, but this reads much more like an argument for string theory research rather than one against it…
A few quick comments, maybe I’ll write something later on my blog about other aspects of the “string theory is just too hard” idea.
1. “understanding particle physics beyond the Standard Model was never the primary motivation of most string theorists anyway”
It really isn’t true that what happened in 1984 was all about the sudden appearance of an excellent theory of quantum gravity. Take a look at the highly cited papers from that era, and you’ll find little about quantum gravity, but a lot about compactification schemes for getting the Standard model. The people who made string theory a hot subject were mostly particle theorists excited by the the idea of a unified theory, with real predictions seemingly possible by looking at the lowest energy states of a superstring propagating on a compactified 10d space-time. They were well aware that making experimental contact with quantum gravitational effects was almost certainly hopeless, and these were people highly concerned with doing research that did have experimental implications.
It was only much later, as hopes for getting particle theory our of string theory have been conclusively dashed, that there as been a fall-back to the argument that “well, we only really care about quantum gravity, weren’t really serious about that particle physics stuff”
2. The problem with the argument that “all we have to do is understand non-perturbative string theory, but it’s just too hard right now”, is that, based on what we do know about non-perturbative string theory, there is zero evidence that it will produce a viable unified model. The situation is quite the opposite: everything that has been learned about non-perturbative effects gives evidence against this, pointing strongly to the conclusion that if any ground states of such a theory lead to a physically sensible theory, an essentially infinite number do, giving a radically non-predictive framework that can’t ever tell you anything about particle physics. This situation is what is driving string theorists into the arms of Lenny Susskind and pseudo-science. The idea that, if we were smart enough, we’d figure out some wonderful new version of M-theory which would explain particle physics has nothing behind it other than wishful thinking.
Charlie,
The problem with announcing that “string theory is mathematics” is that mathematicians aren’t going to agree to this. As Sean points out, no one even knows what “string theory” is supposed to be, it’s not something well-defined, but a set of conjectures and hopes, many with little backing, about a theory that some people would like to exist.
Physicists are all too willing to dismiss the failure of string theory as due to it being too abstract, and thus “just mathematics”. That’s not the problem with it, the problem is that it’s a wrong idea about unification.
Title fixed! Sorry about that.
Peter, of course there was a lot of excitement about compactifications and the attempt to derive particle physics from string theory. But the reason why people were ever optimistic about string theory as a theory of everything was because gravity was included. Naturally, if you think you have the correct theory of quantum gravity, you’re curious about how it connects to particle physics. But even if that turns out to be difficult, having the correct theory of quantum gravity is still pretty interesting.
And Charlie, proclamations aside, string theory is physics. It’s a formal hypothesis about how the real world works. Our difficulties in connecting it with observations don’t change its epistemological status.
This point should probably be included in the argument:
String theory has failed as a theory of everything because it cannot describe what we know about our universe more succinctly then GR and the standard model can. As Peter points out, people used to think the known particle spectrum was going to come out of strings naturally. But it didn’t. In order to make contact with GR and the standard model — as any ToE must — string theory requires all sorts of baroque mathematical convolutions and assumptions, as well as many additional parameters. It is much more complicated than what it is striving to explain. This is a clear sign of a failed theory.
having the correct theory of quantum gravity is still pretty interesting.
Again with the unproven assumptions… and again I say, prove it.
It might be easier to specifically argue against the Landscape.
When the discussion moves from empirical science to pure philosophy, it isn’t correct to assume that scientists are good philosophers. You can find any number of brilliant scientists, now and in history, who can seamlessly move their thoughts from a realm of pure empiricism to pure gobbledy-gook. I know there is no substance to it because you can find many completely opposite directions to the conclusions, and the character of the discussions starts to resemble a religious argument, and we know how productive those are at determining the objective truth. All individuals should recognize that they aren’t immune to the human tendency to start thinking in these directions when the possibility of evidence disappears.
Some things in the universe, including the Cosmological Constant, seem exceptionally tuned. We don’t know why (yet). If String Theory is the ultimate description of the universe, there is reason to suppose we will never know why. The scientific discussion should end there, and now it’s philosophically anyone’s game. Yes, we know of many specific cases where things are exceptionally tuned and we can observe that there is actually a larger landscape of possibilities. It’s not now correct to take this as “evidence” that a landscape of universes “actually” exists. It’s not evidence in any scientific sense, and the supposition is completely equivalent to “it just is”. I’m sorry, but you guys are far smarter than me, but ability and science in science does not project over to pure philosophy any more than it does to politics and policy discussions.
Garrett,
String theory has not ‘failed’ no matter how many times this bit of propaganda is repeated. It is actually very easy to get models which are very close to the Standard Model by straightforward and simple compactifications, either heterotic or Type II. The whole problem of the landscape is that these compactifications are not unique, at least at the level of perturbative string theory. One would have the same problem in any conventional GUT, say in trying to obtain the standard model from E_8.
Peter Woit said: “…. in 1984 … the highly cited papers from that era …[had]… a lot about compactification schemes for getting the Standard model. The people who made string theory a hot subject were mostly particle theorists excited by the the idea of a unified theory, with real predictions seemingly possible …”.
Sean disgreed, saying: “… the reason why people were ever optimistic about string theory as a theory of everything was because gravity was included …”.
You can judge for yourself which is the more accurate view,
based on the following:
At the 1984 APS DPF Santa Fe meeting, John Schwarz gave a talk
(on work with Shahram Hamidi) entitled
“A Unique Unified Theory That Could Be Finite And Realistic”,
in which he discussed “SO(32) and E8xE8 superstrings” with respect to finding “the correct low-energy (compared to the Planck mass) theory in four dimensions with which to make contact”.
Swarz went on to say that “In collaboration with J. Patera, we have classified all the chiral N=1 theories that satisfy the one-loop (and hence two-loop) finiteness conditions. The list includes theories based on E6, SO(10), SU(5), and SU(6) that can describe three or more families without mirror partners.
However, if we also require the occurrence of elementary Higgs fields in representations that can give realistic symmetry-breaking patterns, then one unique scheme is singled out. …
The unique model that is potentially finite and realistic is based on the gauge group SU(5).
… The three-loop calculation could result in a dramatic failure and is therefore of utmost importance. …”.
After Schwarz made his 1984 Santa Fe talk, a lot of work was done on that SU(5) structure. For example,in Physics Letters B, Volume 160, Issues 4-5 , 10 October 1985, Pages 267-270, D. R. T. Jones and A. J. Parkes wrote a paper entitled
“Search for a three-loop-finite chiral theory”. Its abstract stated:
“Grand-unified theories have been constructed out of supersymmetric SU5 theories which are finite at one and two loops. We investigate the three-loop divergences in these models and find that they can never be three-loop finite …”
Despite Schwarz’s declaration that his 1984 superstring theory was predictive and testable,
he did not admit defeat upon failure to pass the three-loop test.
His concrete testable superstring theory just morphed into something harder to test,
and since then, whenever superstring theory has failed a test (such as specific searches for supersymmetric partners, etc) it has continued to morph into more and more vagueness (as of now the Landscape),
with its supporters saying such things as that it “… gives us pieces of the theory of everything. All of the pieces have yet to be put together and some remain unknown. …” and that it is “… part of a larger structure that we don’t understand nearly well enough to make contact with the real world as yet …”.
At the same time, models (such as mine) that actually are predictive and testable (and substantially consistent with observations of particle masses, force strengths, and the Dark Energy : Dark Matter : Ordinary Matter ratio) are ignored and even blacklisted from the Cornell arXiv.
Tony Smith
I don’t think it is convincing enough. The conclusion that one OUGHT to draw from your very nice discussion above, Sean, is that String theorists must be very careful , especially when they report a new result. Unless they come up with a sensible way to test string theory AND show that they understand the larger theory, they shouldn’t claim to.
I have a clear memory as a graduate student in at Brandeis university in the late 80’s (1988 I believe) attending Witten’s series of String Theory lectures at Harvard. The subway lines near Cambridge were so clogged from MIT, Brandeis and other academia traffic for this rockstar event that I remember having to walk the last several blocks to get to Harvard.
On arriving to the campus, the event organizers had to re-schedule the venue from a small lecture room to the large public lecture hall.
My clear recollection was that this buzz was because string theory was promising to “predict” the numeric values for fundamental constants in the standard model (such as electron mass, mixing angle, etc.). Gravity was mentioned as further “bonus” of this theory, but definitely particle physics was a main selling point.
I think anyone who recalls their initial interest in the subject has to admit the promise and hype, and yes what made it so alluring to young graduate students in the 80’s, was much more than just quantum gravity.
Look, I could tell similar stories about people being excited about quantum gravity, and collect all sorts of testimony to back me up. Here’s the thing: it makes absolutely no difference. If Einstein had claimed that GR would lead to an inexhaustible supply of free energy, it would not have affected the truth or falsity or promise of the the theory in the least. The foibles of theorists should not be confused for the problems of theories. Talking about the sociology of physics is interesting in its own right, but has no bearing at all on whether a particular theory is promising or not.
The chief benefit of string theory research as I see it is that it may be starting to yield insights into how to understand strongly coupled dynamics of the sort relevant for QCD. Zeus forbid that the LHC discovers new strongly coupled physics at the TeV scale—that would really piss me off.
Sean,
This is not a question of sociology. It’s about what’s testable science and what isn’t. There were all sorts of reasons people decided to work on string theory, but by far the most important one is that it held out the promise of making real, testable predictions. The problem with pursuing string theory as only a theory of quantum gravity is that it’s not testable. If you believe all the things string theorists would like to be true, not only do they have a consistent theory of quantum gravity, they have an exponentially large number of them. And no way at all to ever test any of them. You can go on about how this makes “absolutely no difference”, that it has nothing to do with the truth or falsity of the theory, but what it has to do with is whether this is legitimate science or not. While an increasingly large number of theorists don’t seem to think this anymore, most scientists are of the opinion that theories that inherently can’t be tested aren’t what science is about.
The question of why individual scientists in the 1980’s were excited about string theory is certainly a question of sociology. We may argue whether one or another reason is a good one or not, but that is a logically distinct question. If we wanted to drop discussions about what such-and-such a person was thinking when they gave a talk twenty years ago, I’d be all in favor of it.
As usual, it does not occur to string advocates that string theory is the wrong theory of quantum gravity, because there are better and more physical ideas. To see how QFT must be modified to work with gravity, one can argue like this:
Every experiment is an interaction between a system and a detector, and the result depends on the physical properties of both. We are typically only interested in the detector-independent part of the result, which is what theories like QFT speak about. QFT never mentions the detector’s properties, because it implicitly assumes that its charge is very small (so the detector does not perturb the system) and its mass is very large (so the detector follows a well-defined classical worldline, i.e. its position and velocity, as measured by physical rods and clocks, commute). This hidden assumption runs into problem specifically with gravity, because then charge and mass are the same (heavy mass = inert mass).
It follows that any theory which implicitly assumes an infinite detector mass, whether it involves fields, particles, strings, loops or whatnot, will run into trouble with gravity, because an infinitely massive detector will interact with gravity and collapse into a black hole. The solution is in principle simple: the theory of quantum gravity must explicitly depend on the detector’s mass.
Incidentally, I have used string theory to make a falsifiable prediction about the LHC.
I’ve finally figured out why I don’t like your “argument”. You make the blanket statement “The best reason to think that research on string theory is largely a waste of time is because it’s just too hard.” This strikes me as like when people say, eg, “I’m a failure” when they want someone to turn around and say “No you’re not.” (or in this case “No, you should think about hard stuff”). Now this is a good “debating tactic” but I’m think a more convincing “real argument” would be to be more precise about what precisely about the thinking task is “too difficult”.