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
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
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
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.
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
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.