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.
