by Lee Smolin
Part of the reason string theory makes no new predictions is that it appears to come in an infinite number of versions. Even if we restrict ourselves to theories that agree with some basic observed facts about our universe, such as its vast size and the existence of the dark energy, we are left with as many as 10500 distinct string theories—that’s 1 with 500 zeros after it, more than all the atoms in the known universe. With such a vast number of theories, there is little hope that we can identify an outcome of an experiment that would not be encompassed by one of them. Thus, no matter what the experiments show, string theory cannot be disproved. But the reverse also holds: No experiment will ever be able to prove it true.
At the same time, we understand very little about most of these string theories. And of the small number we do understand in any detail, every single one disagrees with the present experimental data, usually in at least two ways.
So we face a paradox. Those string theories we know how to study are known to be wrong. Those we cannot study are thought to exist in such vast numbers that no conceivable experiment could ever disagree with all of them.
These are not the only problems. String theory rests on several key conjectures, for which there is some evidence but no proof. Even worse, after all the scientific labor expended in its study, we still do not know whether there is a complete and coherent theory that can even go by the name “string theory.” What we have, in fact, is not a theory at all but a large collection of approximate calculations, together with a web of conjectures that, if true, point to the existence of a theory. But that theory has never actually been written down. We don’t know what its fundamental principles are. We don’t know what mathematical language it should be expressed in—perhaps a new one will have to be invented to describe it. Lacking both fundamental principles and the mathematical formulation, we cannot say that we even know what string theory asserts.
Here is how the string theorist Brian Greene puts it in his latest book, The Fabric of the Cosmos: “Even today, more than three decades after its initial articulation, most string practitioners believe we still don’t have a comprehensive answer to the rudimentary question, What is string theory? . . . [M]ost researchers feel that our current formulation of string theory still lacks the kind of core principle we find at the heart of other major advances.”2
Gerard ’t Hooft, a Nobel Prize winner for his work in elementary-particle physics, has characterized the state of string theory this way: “Actually, I would not even be prepared to call string theory a ‘theory,’ rather a ‘model,’ or not even that: just a hunch. After all, a theory should come with instructions on how to deal with it to identify the things one wishes to describe, in our case the elementary particles, and one should, at least in principle, be able to formulate the rules for calculating the properties of these particles, and how to make new predictions for them. Imagine that I give you a chair, while explaining that the legs are still missing, and that the seat, back and armrest will perhaps be delivered soon. Whatever I did give you, can I still call it a chair?”3
David Gross, a Nobel laureate for his work on the standard model, has since become one of the most aggressive and formidable champions of string theory. Yet he closed a recent conference intended to celebrate the theory’s progress by saying, “We don’t know what we are talking about. . . . The state of physics today is like it was when we were mystified by radioactivity. . . . They were missing something absolutely fundamental. We are missing perhaps something as profound as they were back then.”4
But though string theory is so incomplete that its very existence is an unproved conjecture, that does not keep many who work on it from believing that it is the only way forward for theoretical physics. One prominent string theorist, Joseph Polchinski, of the Kavli Institute for Theoretical Physics at UC Santa Barbara, was asked not long ago to give a talk on “Alternatives to String Theory.” His first reaction, he said, “was that this was silly, there are no alternatives. . . . All good ideas are part of string theory.”5 Lubos Motl, an assistant professor at Harvard, recently asserted on his blog that “the most likely reason why no . . . person has convinced others about [an] alternative to string theory is that there probably exists no alternative to string theory.”6
What is going on here? Usually in science one means something quite definite by the term theory. Lisa Randall, an influential particle theorist and Motl’s colleague at Harvard, defines a theory as “a definite physical framework embodied in a set of fundamental assumptions about the world—and an economical framework that encompasses a wide variety of phenomena. A theory yields a specific set of equations and predictions—ones that are borne out by successful agreement with experimental results.”7
String theory does not fit this description—at least not yet. How, then, are some experts sure there is no alternative to string theory, if they don’t know precisely what it is? What exactly is it that they are sure has no alternative? These are some of the questions that led me to write this book.
Theoretical physics is hard. Very hard. Not because a certain amount of math is involved but because it involves great risks. As we will see over and over again as we examine the story of contemporary physics, science of this kind cannot be done without risk. If a large number of people have worked on a question for many years and the answer remains unknown, it may mean that the answer is not easy or obvious. Or this may be a question that has no answer.
String theory, to the extent it is understood, posits that the world is fundamentally different from the world we know. If string theory is right, the world has more dimensions and many more particles and forces than we have so far observed. Many string theorists talk and write as if the existence of those extra dimensions and particles were an assured fact, one that no good scientist can doubt. More than once, a string theorist has said to me something like “But do you mean you think it’s possible that there are not extra dimensions?” In fact, neither theory nor experiment offers any evidence at all that extra dimensions exist. One of the goals of this book is to demystify the claims of string theory. The ideas are beautiful and well motivated. But to understand why they have not led to greater progress, we have to be clear about exactly what the evidence supports and what is still missing.
Because string theory is such a high-risk venture—unsupported by experiment, though very generously supported by the academic and scientific communities—there are only two ways the story can end. If string theory turns out to be right, string theorists will turn out to be the greatest heroes in the history of science. On the basis of a handful of clues—none of which has an unambiguous reading—they will have discovered that reality is far more vast than previously imagined. Columbus discovered a new continent unknown to the king and queen of Spain (as the Spanish royals were unknown to the residents of the New World). Galileo discovered new stars and moons, and later astronomers discovered new planets. All this would pale in the face of the discovery of new dimensions. Moreover, many string theorists believe that the myriad worlds described by the huge number of string theories really do exist—as other universes impossible for us to see directly. If they are right, we see far less of reality than any group of cave dwellers saw of the earth. No one in human history has ever guessed correctly about such a large expansion of the known world.
On the other hand, if string theorists are wrong, they can’t be just a little wrong. If the new dimensions and symmetries do not exist, then we will count string theorists among science’s greatest failures, like those who continued to work on Ptolemaic epicycles while Kepler and Galileo forged ahead. Theirs will be a cautionary tale of how not to do science, how not to let theoretical conjecture get so far beyond the limits of what can rationally be argued that one starts engaging in fantasy.
One result of the rise of string theory is that the community of people who work on fundamental physics is split. Many scientists continue to work on string theory, and perhaps as many as fifty new PhDs are awarded each year for work in t
his field. But there are some physicists who are deeply skeptical—who either never saw the point or have by now given up waiting for a sign that the theory has a consistent formulation or makes a real experimental prediction. The split is not always friendly. Doubts are expressed on each side about the professional competence and ethical standards of the other, and it is real work maintaining friendships across the divide.
According to the picture of science we all learned in school, situations like this are not supposed to develop. The whole point of modern science, we are taught, is that there is a method that leads to progress in our understanding of nature. Disagreement and controversy are of course necessary for science to progress, but there is always supposed to be a way to resolve a dispute by means of experiment or mathematics. In the case of string theory, however, this mechanism seems to have broken down. Many adherents and critics of string theory are so confirmed in their views that it is difficult to have a cordial discussion on the issue, even among friends. “How can you not see the beauty of the theory? How could a theory do all this and not be true?” say the string theorists. This provokes an equally heated response from skeptics: “Have you lost your mind? How can you believe so strongly in any theory in the complete absence of experimental test? Have you forgotten how science is supposed to work? How can you be so sure you are right when you do not even know what the theory is?”
I have written this book in the hope that it will contribute to an honest and useful discussion among experts and lay readers alike. In spite of what I have seen in the last few years, I believe in science. I believe in the ability of the scientific community to rise above acrimony and resolve controversy through rational argument based on the evidence in front of us. I am aware that just by raising these issues, I will anger some of my friends and colleagues who work on string theory. I can only insist that I am writing this book not to attack string theory or those who believe in it but out of admiration for them and, above all, as an expression of faith in the physics scientific community.
So this is not a book about “us” versus “them.” During my career, I have worked on both string theory and on other approaches to quantum gravity (the reconciliation of Einstein’s general theory of relativity with quantum theory). Even if most of my efforts have gone into these other approaches, there have been periods when I avidly believed in string theory and devoted myself to solving its key problems. While I didn’t solve them, I wrote eighteen papers in the subject; thus, the mistakes I will discuss are my mistakes as much as anyone else’s. I will speak of conjectures that were widely believed to be true, in spite of never having been proved. But I was among the believers, and I made choices about my research based on those beliefs. I will speak of the pressures that young scientists feel to pursue topics sanctioned by the mainstream in order to have a decent career. I have felt those pressures myself, and there were times when I let my career be guided by them. The conflict between the need to make scientific judgments independently and make them in a way that doesn’t alienate you from the mainstream is one that I, too, have experienced. I write this book not to criticize scientists who have made choices different from mine but to examine why scientists need to be confronted with such choices at all.
In fact, it took me a long time to decide to write this book. I personally dislike conflict and confrontation. After all, in the kind of science we do, anything worth doing is a risk and all that really matters is what our students’ students will think worthy of teaching their own students fifty years down the road. I kept hoping someone in the center of string-theory research would write an objective and detailed critique of exactly what has and has not been achieved by the theory. That hasn’t happened.
One reason to take these issues public goes back to the debate that took place a few years ago between scientists and “social constructivists,” a group of humanities and social science professors, over how science works. The social constructivists claimed that the scientific community is no more rational or objective than any other community of human beings. This is not how most scientists view science. We tell our students that belief in a scientific theory must always be based on an objective evaluation of the evidence. Our opponents in the debate argued that our claims about how science works were mainly propaganda designed to intimidate people into giving us power, and that the whole scientific enterprise was driven by the same political and sociological forces that drove people in other fields.
One of the main arguments we scientists used in that debate was that our community was different because we governed ourselves according to high standards—standards that prevented us from embracing any theory until it had been proved, by means of published calculations and experimental data, beyond the doubt of a competent professional. As I will relate in some detail, this is not always the case in string theory. Despite the absence of experimental support and precise formulation, the theory is believed by some of its adherents with a certainty that seems emotional rather than rational.
The aggressive promotion of string theory has led to its becoming the primary avenue for exploring the big questions in physics. Nearly every particle theorist with a permanent position at the prestigious Institute for Advanced Study, including the director, is a string theorist; the exception is a person hired decades ago. The same is true of the Kavli Institute for Theoretical Physics. Eight of the nine MacArthur Fellowships awarded to particle physicists since the beginning of the program in 1981 have also gone to string theorists. And in the country’s top physics departments (Berkeley, Caltech, Harvard, MIT, Princeton, and Stanford), twenty out of the twenty-two tenured professors in particle physics who received PhDs after 1981 made their reputation in string theory or related approaches.
String theory now has such a dominant position in the academy that it is practically career suicide for young theoretical physicists not to join the field. Even in areas where string theory makes no predictions, like cosmology and particle phenomenology, it is common for researchers to begin talks and papers by asserting a belief that their work will be derivable from string theory sometime in the future.
There are good reasons to take string theory seriously as a hypothesis about nature, but this is not the same as declaring its truth. I invested several years of work in string theory because I believed in it enough to want to try my hand at solving its key problems. I also believed that I had no right to an opinion until I knew it in detail, as only a practitioner could. At the same time, I have worked on other approaches that also promise to answer fundamental questions. As a result, I’m regarded with some suspicion by people on both sides of the debate. Some string theorists consider me “anti-string.” This couldn’t be less true. I would never have put so much time and effort into working on string theory, or written three books largely motivated by its problems, if I wasn’t fascinated by it and didn’t feel that it might turn out to be part of the truth. Nor am I for anything except science, or against anything except that which threatens science.
But there’s more at stake than amity among colleagues. To do our work, we physicists require significant resources, which are provided largely by our fellow citizens—through taxes as well as foundation money. In exchange, they ask only for the chance to look over our shoulders as we forge ahead and deepen humanity’s knowledge of the world we share. Those physicists who communicate with the public, whether through writing, public speaking, television, or the Internet, have a responsibility to tell the story straight. We must be careful to present the failures along with the successes. Indeed, being honest about failures is likely to help rather than hurt our cause. After all, the people who support us live in the real world. They know that progress in any endeavor requires that real risks be taken, that sometimes you will fail.
In recent years, many books and magazine articles for the general public have described the amazing new ideas that theoretical physicists have been working on. Some of these chronicles have been less than careful about explaining just how far the new
ideas are from both experimental test and mathematical proof. Having benefited from the public’s desire to know how the universe works, I feel a responsibility to make sure that the story told in this book sticks close to the facts. I hope to lay out the various problems we have been unable to solve, explain clearly what experiment supports and doesn’t support, and distinguish fact from speculation and intellectual fad.
Above all, we physicists have a responsibility to the future of our craft. Science, as I shall argue later, is based on an ethic, and that ethic requires good faith on the part of its practitioners. It also requires that each scientist be the judge of what he or she believes, so that every unproved idea is met with a healthy dose of skepticism and criticism until it is proved. This, in turn, requires that a diversity of approaches to unsolved problems be supported and welcomed into the community of science. We do research because even the smartest among us doesn’t know the answer. Often it lies in a direction other than the one pursued by the mainstream. In those cases, and even when the mainstream guesses right, the progress of science depends on healthy support for scientists who hold divergent views.
Science requires a delicate balance between conformity and variety. Because it is so easy to fool ourselves, because the answers are unknown, experts, no matter how well trained or smart, will disagree about which approach is most likely to yield fruit. Therefore, if science is to move forward, the scientific community must support a variety of approaches to any one problem.
There is ample evidence that these basic principles are no longer being followed in the case of fundamental physics. While few would disagree with the rhetoric of diverse views, it is being practiced less and less. Some young string theorists have told me that they feel constrained to work on string theory whether or not they believe in it, because it is perceived as the ticket to a professorship at a university. And they are right: In the United States, theorists who pursue approaches to fundamental physics other than string theory have almost no career opportunities. In the last fifteen years, there have been a total of three assistant professors appointed to American research universities who work on approaches to quantum gravity other than string theory, and these appointments were all to a single research group. Even as string theory struggles on the scientific side, it has triumphed within the academy.
