Dear Friends and Colleagues,

A number of people have asked me to clarify my views concerning string theory, as discussed in my recent book, The Trouble with Physics. I am happy to do so as there has been some misquotation and misattributions of my views,  which do not reflect a reading of what the book actually says.  Indeed, most readers and most reviewers  have said they find TTWP balanced, accurate and reasonable.  Some readers, including several physics students, have told me that reading TTWP increased their interest in string theory.  But a small number of people have attributed views to me that are far more negative towards string theory than my actual views, as expressed in my three books and other writings.    This is disturbing for me,  because I consider many string theorists to be friends, and also because I would prefer to spend my time in a constructive debate over what the book actually says rather than responding to criticism based on distortions of the book’s content.   I worked hard to write a book that was fair, accurate and constructive and I have been uncomfortable that some of the discussion has focuses on issues other than the actual text of what I wrote.  

Let me start by saying that I do not think and do not write that that research on string theory should cease or that string theorists should no longer be funded or hired. As I say in Chapter  12:  “String theory succeeds at enough things so that it is reasonable to hope that parts of it, or perhaps something like it, might comprise some future theory.  So string theory is certainly among the directions that deserve more investigation.” So I am not “against string theory” and any interpretation of my book as an “attack on string theory” is a misreading1 .   

I would have thought that the record of my interest in string theory is clear. I have always strongly supported, and, in some cases, led efforts to hire string theorists. I taught a graduate course in string theory and mentored students and postdocs working in it. I have written myself 18 technical papers in the subject, the last of which was in 2005 and I continue to have work in progress in string theory.  I would not have written these papers, or three books largely devoted to analyzing problems it faces if I did not believe it had a reasonable chance to be part of the truth about nature.  Among the people who work on non-string approaches to quantum gravity, I have made over the years the most substantial investment of time and work in string theory.   Indeed,  given that I have worked on different approaches to quantum gravity throughout my career, I have always had the view that the division of people working on quantum gravity into separate communities based on the approach they take is artificial and counterproductive  scientifically.  

So what is my book against, and what is it for?   TTWP is certainly critical of the view that we know enough about string theory and its alternatives to elevate it above other approaches as “the only game in town” or “the dominant paradigm in theoretical physics.”  My book defends a view in which string theory is one of several  promising approaches towards  unification and quantum gravity.  Thus, TTWP argues that progress in fundamental  physics will be much helped by a more reflective and diverse atmosphere which  embraces  the full range of ideas and approaches, including string theory, that exist in the field.

More specifically, my book has several  aims, which are as follows:



I hope two things are clear from this. First, my attitude towards string theory is that it is deeply promising, while being at the same time presently in crisis.  My aim in writing this book was not to publicize this crisis-several journalists told me this was an old story, already covered for example by Leonard Susskind’s recent book and articles in newspapers and magazines in 2004 and 2005.  It was to try to understand the roots of the crisis in order to help us get out of it.  Second, the historical and philosophical chapters of the book are central to all of its aims, so the book cannot be understood without following the argument through those chapters. For example, I argue it is important, in understanding the landscape problem, to know how it was anticipated in early work on higher dimensional unification.

The core argument of the book is that there are five key problems which must be solved to complete the revolution in physics begun by Einstein-which remain unsolved.  I try to understand why they are so hard to solve while trying to find out how best to proceed to solve them.   String theory plays a prominent role because it is the best developed and most widely studied approach to these problems, but the fact that these problems remain unsolved challenges the whole field.  

With regard to string theory, the issues I discuss are not new and my views on them should not be surprising to people who know my work or previous writings.


Let us take them one at a time.  The landscape issue is one I have already published on extensively,  having been one of the first, if not the first, to recognize the problem and try to think it through.  It was the subject of my first book, The Life of the Cosmos (1997), and related  papers (where the landscape of theories was first introduced). My view as been since the early 90s that, if the landscape, if it is real, represents a challenge that can only be successfully met by finding a way to nevertheless make falsifiable predictions (Thus, I am proud to have been called a Popperazzi!).  This can, I argue in detail, best be achieved through a cosmological scenario that creates a highly non-random ensemble, and hence non-trivial correlations and predictions.     

Also in my first book I explained how the landscape issue is related to the need for a manifestly background independent theory, and argue that it can in the long run only be solved by the construction of such a theory.   In TTWP as well as in previous books and papers I also explain why, in any case, a fundamental theory of quantum gravity must be manifestly  background independent2.  Some of these arguments are very old, and were  given by Leibniz, Mach and Einstein, as well as more recently by Barbour, Stachel, Rovelli and others.  

Some string theorists respond that, if the Maldacena conjecture is true in its strong form, it already gives an example of a partly, or weakly, background independent theory, in that the geometry of six extra dimension would be emergent from a theory with three dimensions of space.  I do acknowledge this in the book, on page3  189 and again on page 240.  At the same time, as I go on to explain,  this does not realize the full meaning of background independence as set out in the arguments of the people mentioned above. This is because the full notion of background independence  requires that  the basic laws can refer to no classical metric or fields, and can involve no global symmetries.   This is not a debating point, it is fundamental  to the reasons why it is argued that a quantum theory of gravity must be background independent.    

The fact is that many workers in quantum gravity are convinced by the need for a manifestly background independent theory. This includes some string theorists (for example,  Brian Greene, as he explains in his second book.)   Indeed, a number of people have tried to construct a manifestly background independent formulation of string theory and there are interesting proposals that could be developed. This is where I have invested several years of work and the goal of my second book, Three Roads, was to argue for this.   

But most people who believe in background independence have pursued it through the study of theories that manifestly have that property.  These include causal dynamical triangulations, loop quantum gravity, spin foam models, causal set models, and some aspects of non-commutative  geometry (as envisioned by Connes.).  The fact is that there has been a lot of progress in these directions the last six years.  String theorists do not help their case by ignoring or minimizing these developments.   One reason is that background independence  may be the key to resolving the problems faced by string theory.   If so, then string theory and the manifestly background independent approaches are not competitors, they are complementary. Both are then  necessary steps on the way to the next correct theory, which implies that practitioners of each have a lot to learn from the other.  This was in fact the theme of my second book, Three Roads.  

With regard to the third point about the unresolved conjectures, my aim is not to argue that they are false. I don’t know if they are true or not.  My point was  that too easy belief in unproven conjectures in any field hurts that field, because it reduces the need to concentrate on proving them.  I was  also concerned about the logic of arguments that take the existence of a fundamental formulation of string theory for granted, rather than evaluating the evidence for that conjecture   So my argument here also is not “anti-string,” it is just anti - taking these conjectures for granted, rather than working hard to resolve them.   If we simply assume they are true we will miss important insights to be gained by proving them, and we also take on unnecessary risk because it is always possible not all are true.  

In part III of the book, I emphasize there are a number of experiments in preparation that will test key ideas in contemporary theoretical physics, including supersymmetry, higher dimensions, quantum cosmology models and modifications of special relativity. These experiments include the LHC, the proposed ILC,  AUGER, GLAST, future CMB observations and others.  The fact that these experiments are in progress provides firm evidence that fundamental physics is healthy and the long period in which important ideas went untested in now coming to and end. This is why TTWP concludes optimistically.

I hope it is clear from this summary why I insist that my book is not an “attack on string theory.”   I discuss the open problems we face, not to attack the theory but to make a constructive contribution by analyzing the historical and philosophical roots of the issues. I also present proposals about what we must do to resolve the current problems, having to do with both background independence and how the landscape issues are to be resolved.  Of course not everyone will agree with these views, but if they want to criticize my book they should at least try to understand the arguments made for the book’s conclusions and respond by finding fault with them.   

There are a few criticisms made of the book that appear to come from people who have not read it. For example, I have heard it said that I fail to emphasize that string theory has had an important impact on other fields, especially pure mathematics and gauge theories.  But I do. To quote from p 177, “No one disputes that a lot of good mathematics has come out of string theory and that our understanding of some gauge theories has been deepened. But the usefulness of spin-offs for mathematics or other areas of physics is not evidence either for or against the correctness  of string theory as a scientific theory.”    So while I do mention these spin offs I do not see how they can be decisive for the question of whether or not string theory succeeds as a fundamental theory of nature.    
Some have suggested I could in this vein mention the very recent applications of string theory to heavy ion physics.  I am happy to do this and will incorporate this in future editions.  

Let me now turn to the sociological and philosophical issues discussed in the book.  A major theme of TTWP is that in situations where we face major unsolved problems, it is wise to foster a diversity of approaches by good scientists towards them.  This means that we encourage and welcome  people to invent and pursue a wide range of approaches.  

The reason I advocate this view is that I am convinced it is crucial for the health of science generally. I give several reasons in support of this view.  Some are philosophical and, as discussed briefly in Chapter 17, have their source in work of philosophers such as  Feyerabend and Popper.   Other reasons are based on historical and contemporary episodes, which are detailed in the book.   Still other reasons follow from an acknowledgement that this kind of research is risky; these can be best expressed in economic terms.  Successful investment bankers do not have a simple view of the market which leads them just to invest in the most popular instruments, they have  instead a sophisticated view of risk that leads them to diversify risk by hedging their investments.   I also argue that having people around with different and competing points of view makes us all work harder and more honestly, while it stimulates us and provides us with a continuous source of new ideas, questions and viewpoints.  Thus, I argue that any research program progresses faster when it is pursued with in the context of a broad and diverse community which includes competing ideas and directions.  

I do believe that these issues are relevant for the questions facing string theory.   I  argue from historical cases that  the progress of research in string theory has been hurt by too narrow of a research agenda, disinterest in developments in alternative and competing research programs and too strict an identification of who is and who is not part of the community of people worth paying attention to.  These include the role of 11dimensional supersymmetry, membranes and the landscape issue, all of which came eventually to be appreciated as keys to string theory, after long periods of being ignored.  I also argue that part of the reason for the difficulties faced by string theory and other approaches to fundamental physics is their reliance on too pragmatic a research style and that an essential contribution is to be made by scientists who work more in the style of Einstein and Bohr, which emphasizes foundational questions and their connections to old philosophical puzzles.

But, in  case it needs to be said, criticism of the sociology of a research community does not contradict a belief in the promise of the theory itself.   It also appears that these sociological issues affect other areas of contemporary science. I have heard and read statements of concern about them from colleagues in other fields such as biology, computer science and economics.   In physics, I suspect that they have been with us for a long time, but they become more significant in periods and fields which lack a close coupling between theory and experiment.  

For this reason, an important part of the book are the proposals it makes for how to resolve these sociological issues. These develop ideas I first put forwards in essays in New Scientist and Physics Today.  The proposals I make about them are not specific to string theory, they are meant generally; I argue that they would improve the rate of progress in many fields.

An example of the kind of proposal I endorse is to set up  “venture capital” funds in science to support new ideas and emerging fields which may not yet have strong institutional support4 . The effective of this should be to increase the diversity of approaches investigated  to key unsolved problems. I also argue that young scientists should be funded and hired based on their promise as future leaders, rather than because they do good incremental work on established problems. I argue that these proposals would benefit all approaches, because any research program, including string theory, will make the most progress, when  its practitioners are embedded within a community that includes a diverse range of approaches to the important unsolved problems.      

This brings me to issues about funding and resources.   In the book I do argue that other approaches to quantum gravity as well as foundations of quantum theory are under-supported.   I make this case on the basis of recent results in these fields, which I argue strongly justifies support for those responsible for these results, as well as on the general argument for diversity of approaches. But to argue that those who work fundamental physics apart from string theory should not pay a price in career opportunities is not the same as saying that funding for string theory should be cut. For one thing supporting fully the small number of people in the field of quantum gravity would not seriously perturb funding priorities in high energy theory, which is a much larger community.  

But, my main point is that it benefits the whole field when young scientists compete on an even playing field, based on their promise and contributions, according to criteria that reward originality and intellectual independence over incremental contributions to established directions.  For one thing it means that young scientists make their decisions about which fields and research programs to contribute to based on their independent analysis of the promise of different approaches, and not because making one choice over another would strongly improve their career opportunities.  Science, I argue, progresses fastest when all scientists feel free to work on directions they think are most promising.  In case it needs to be said, in practice I apply this as much to people working in quantum gravity and foundations of quantum theory as I do to string theory.   

I also argue that room should be made in the academic world for the small number of deep thinkers whose work consists of probing the deep problems in the definition of space-time or the foundations of quantum theory.  I argue by example that these very independent thinkers make contributions to the solutions of fundamental problems of the kind needed to help us resolve the issues we presently face.   There are so few such people, and their contributions have over time proved so essential, I find it difficult to understand how initiatives to support them could be controversial.  

In closing, let me say two things.  First, as I describe in my book, there are strong arguments coming from the history and philosophy of science that controversy and disagreement among experts about key unsolved problems is not only a sign of health in science, it is necessary to the processes by which science makes progress.  So the fact that there is a debate about issues such as the landscape, background independence, higher dimensions etc is a sign that fundamental  theoretical  physics is healthy.  It is a very good sign, indeed, that not only is there debate, there are competing research programs which explore different possible directions for the next big unification in physics.  

Second, in spite of these signs of health, and the upcoming experimental tests of competing ideas, the support for fundamental theoretical physics in the United States, coming from public and private foundations, is far from generous.  The result is that some of the very brightest scientists on the planet, both newcomers and  accomplished scientists, are competing for ever scarcer resources.  This is especially unfortunate given the fact that the level of talent and enthusiasm of young scientists entering theoretical physics has never been higher.  Given the key role that fundamental science plays in economic development, and the challenges from China, Europe and elsewhere to North American  leadership in science and technology, this is a time when the facts justify large increases in support for fundamental physics.  


                Sincerely yours,


                Lee Smolin

_________

1  Some people seem to have gotten this impression, not from my book, but from the cover, publicity materials or things said in reviews.    I was surprised that the cover would become an issue, certainly it was more provocative than it would have been had I had control over it. I am sorry about this.  But at the same time,  it is just a cover and I would hope that people interested in what  the book  has to say would read it.  The fact that authors do not always have  control over cover and advertising copy, and how we are quoted by journalists, raises issues that would be interesting to discuss, but I would ask that we  be fair and discuss them in the context of how all the  books on this subject were portrayed and presented.  But this is not the subject of this letter, which concerns the text that I wrote.  

2  The use of “manifestly” here was suggested by Brian Greene to distinguish the form of background independence long advocated by people in quantum gravity from the weaker, partial form relevant for AdS/CFT.  I am happy to adopt it for emphasis, but to avoid  muddying the scientific issue it seems easier to let the words “background independence” continue to refer to what they always have  and introduce a new phrase “weak background independence” for the new version relevant for AdS/CFT. 

3  Here are the quotes: On page 189: ”…if the strong form of the Maldacena conjecture turns out to be true — which is also consistent with the present evidence — then string theory provides good quantum theories of gravity, in the special case of backgrounds with a negative cosmological constant. Moreover, those theories would be partly background-independent, in that   a nine-dimensional space is generated from physics in a three-dimensional space.…There is other evidence that string theory can provide a unification  of gravity with quantum theory…”

On page 240 I repeated the point:  “In a certain limited sense, if the strong form of the Maldacena conjecture (see chapter 9) turns out to be true, a nine-dimensional geometry will emerge out of a fixed three-dimensional geometry. It is thus not surprising to hear Edward Witten say, as he did in a recent talk at the Kavli Institute for Theoretical Physics at UC Santa Barbara, that “most string theorists suspect that spacetime is an ‘emergent phenomenon,’ in the language of condensed matter physics...”

4  This proposal has been developed by Eric Weinstein, from whom I have learned a lot about the application of economic methods to the issues raised in the book.