MACROSCOPE

# Is String Theory Even Wrong?

For nearly 18 years now, most advanced mathematical work in
theoretical particle physics has centered on something known as
string theory. This theory is built on the idea that elementary
particles are not pointlike objects but are the vibration modes of
one-dimensional "stringlike" entities. This formulation
hopes to do away with certain lingering problems in fundamental
particle physics and to offer the possibility of soon explaining
*all* physical phenomenaýeverything from neutrinos to
black holesýwith a single theory. Fifteen years ago Edward
Witten of the Institute for Advanced Study made the widely quoted
claim that "string theory is a part of 21st-century physics
that fell by chance into the 20th century,"** **so
perhaps it is now time to begin judging the success or failure of
this new way of thinking about particle physics.

The strongest scientific argument in favor of string theory is that it appears to contain a theory of gravity embedded within it and thus may provide a solution to the thorny problem of reconciling Einstein's general relativity with quantum mechanics and the rest of particle physics. There are, however, two fundamental problems, which are hard to get around.

First, string theory predicts that the world has 10 space-time dimensions, in serious disagreement with all the evidence of one's senses. Matching string theory with reality requires that one postulate six unobserved spatial dimensions of very small size wrapped up in one way or another. All the predictions of the theory depend on how you do this, but there are an infinite number of possible choices, and no one has any idea how to determine which is correct.

The second concern is that even the part of string theory that is understood is internally inconsistent. This aspect of the theory relies on a series expansion, an infinite number of terms that one is supposed to sum together to get a result. Whereas each of the terms in the series is probably finite, their sum is almost certainly infinite. String theorists actually consider this inconsistency to be a virtue, because otherwise they would have an infinite number of consistent theories of gravity on their hands (one for each way of wrapping up six dimensions), with no principle for choosing among them.

The "M" Word

These two problems have been around since the earliest work on
string theoryýalong with the hope that they would somehow
cancel each other out. Perhaps some larger theory exists to which
string theory is just an approximate solution obtained by series
expansion, and this larger theory will explain what's going on with
the six dimensions we can't see. The latest version of this vision
goes under the name of "M-theory," where the "M"
is said variously to stand for "Membrane,"
"Matrix," "Mother," "Meta,"
"Magic" or "Mystery"ýalthough
"Mythical" may be more appropriate, given that nearly
eight years of work on this idea have yet to lead to even a good
conjecture about what M-theory might be.** **

The reigning Standard Model of particle physics, which string theory attempts to encompass, involves at its core certain geometrical concepts, namely the Dirac operator and gauge fields, which are among the deepest and most powerful ideas in modern mathematics. In string theory, the Dirac operator and gauge fields are not fundamental: They are artifacts of taking a low-energy limit. String theorists ask mathematicians to believe in the existence of some wonderful new sort of geometry that will eventually provide an explanation for M-theory. But without a serious proposal for the underlying new geometry, this argument is unconvincing.

The experimental situation is similarly bleak. It is best described by Wolfgang Pauli's famous phrase, "It's not even wrong." String theory not only makes no predictions about physical phenomena at experimentally accessible energies, it makes no precise predictions whatsoever. Even if someone were to figure out tomorrow how to build an accelerator capable of reaching the astronomically high energies at which particles are no longer supposed to appear as points, string theorists would be able to do no better than give qualitative guesses about what such a machine might show. At the moment string theory cannot be falsified by any conceivable experimental result.

There is, however, one physical prediction that string theory does make: the value of a quantity called the cosmological constant (a measure of the energy of the vacuum). Recent observations of distant supernovae indicate that this quantity is very small but not zero. A simple argument in string theory indicates that the cosmological constant should be at least around 55 orders of magnitude larger than the observed value. This is perhaps the most incorrect experimental prediction ever made by any physical theory that anyone has taken seriously.

With such a dramatic lack of experimental support, string theorists often attempt to make an aesthetic argument, professing that the theory is strikingly "elegant" or "beautiful." Because there is no well-defined theory to judge, it's hard to know what to make of these assertions, and one is reminded of another quotation from Pauli. Annoyed by Werner Heisenberg's claims that, though lacking in some specifics, he had a wonderful unified theory (he didn't), Pauli sent letters to some of his physicist friends each containing a blank rectangle and the text, "This is to show the world that I can paint like Titian. Only technical details are missing." Because no one knows what "M-theory" is, its beauty is that of Pauli's painting. Even if a consistent M-theory can be found, it may very well turn out to be something of great complexity and ugliness.

What exactly *can* be said for string theory? In recent
years, something called the Maldacena conjecture has led to some
success in using string theory as a tool in understanding certain
quantum field theories that don't include gravity. Mathematically,
string theory has covered a lot of ground over the past 18 years and
has led to many impressive new results. The concept of "mirror
symmetry" has been very fruitful in algebraic geometry, and
conformal field theory has opened up a new, fascinating and very
deep area of mathematics. Unfortunately for physics, these
mathematically interesting parts of string theory do little to
connect it with the real world.

String theory has, however, been spectacularly successful on one
frontýpublic relations. For example, it's been the subject of
the best-selling popular science book of the past couple years:
*The Elegant Universe* by Brian Greene, one of my
colleagues at Columbia. The National Science Foundation is funding a
series of *NOVA* programs based on his accessible and
inspiring book. What is more, the Institute for Theoretical Physics
at the University of California, Santa Barbara, organized last
spring** **a conference to train high school
teachers in string theory so that they can teach it to their
students. And *The* *New York Times* and other popular
publications regularly run articles on the latest developments in
string theory.

It's easy enough to see why the general public is taken with string theory, but one wonders why so many particle theorists are committed to working on it. Sheldon Glashow, a string-theory skeptic and Nobel-laureate physicist at Harvard, describes string theory as "the only game in town." Why this is so perhaps has something to do with the sociology of physics.

During much of the 20th century there were times when theoretical particle physics was conducted quite successfully in a somewhat faddish manner. That is, there was often only one game in town. Experimentalists regularly discovered new and unexpected phenomena, each time leading to a flurry of theoretical activity (and sometimes to Nobel prizes). This pattern ended in the mid-'70s with the overwhelming experimental confirmation and widespread acceptance of the Standard Model of particle physics. Since then, particle physics has been a victim of its own success, with theoreticians looking for the next fad to pursueýand finding it in string theory.

One reason that only one new theory has blossomed is that graduate students, postdocs and untenured junior faculty interested in speculative areas of mathematical physics beyond the Standard Model are under tremendous pressures. For them, the idea of starting to work on an untested new idea that may very well fail looks a lot like a quick route to professional suicide. So some people who do not believe in string theory work on it anyway. They may be intimidated by the fact that certain leading string theorists are undeniably geniuses. Another motivation is the natural desire to maintain a job, get grants, go to conferences and generally have an intellectual community in which to participate. Hence, few stray very far from the main line of inquiry.

Affirmative Actions

What can be done to inject more diversity of thought into this great quest of theoretical physics? Even granting that string theory is an idea that deserves to be developed, how can people be encouraged to come up with promising alternatives? I would argue that a good first step would be for string theorists to acknowledge publicly the problems and cease their tireless efforts to sell this questionable theory to secondary school teachers, science reporters and program officers.

The development of competing approaches will require senior string theorists to consider working on less popular ideas and begin encouraging their graduate students and postdocs to do the same. Instead of trying to hire people working on the latest string-theory fad, theory groups and funding agencies could try to identify young mathematical physicists who are exploring completely different avenues. (Pushing 45, I no longer qualify.) Finding ways to support such people over the long term would give them a much-needed chance to make progress.

Although I am skeptical of science writer John Horgan's pessimistic notion that physics is reaching an end, the past 15 years of research in particle theory make depressingly clear one form such an end could take: a perpetual, well-promoted but never-successful investigation of a theory that has no connection with the physical world. If only physicists have the will to abandon a failed project and start looking for some new ideas, this sad fate can be avoided.

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