Response to Criticism

TTWP has raised lively discussion and comment. While the book speaks for itself, there are some criticisms and queries which have been made that I would like to respond to.

LETTER

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:

• To give a constructive analysis of the present situation in
  fundamental physics, in order to better understand how best to
  proceed from here. To me the present situation is a puzzle: we
  have a theory of unification and quantum gravity with great promise and
  yet it appears we are unable to make falsifiable predictions for doable
  experiments. Thus, in Part II I give as much space to
  establishing the reasons for enthusiasm about string theory as I do to
  detailing open issues and unsolved problems. To gain a basis for
  understanding the present situation, I examine the historical and
  philosophical roots of the search for a unified theory. For me,
  key sections of the book are the historical chapters in Part I
  and the chapter on methodology of science (17) because they provide
  perspectives against which to evaluate the present situation.
• To propose a solution to the questions of what science is and why it is successful.
• To propose a solution to the sociological puzzle of why it is
  that we have different approaches to the problem of quantum gravity
  being pursued by distinct communities which have little communication
  between them.
• To address the claims made since 2003, in response to the
  landscape, that the criteria of falsification is too strict or
  can be replaced by the anthropic principle.
• To describe several recent experimental and theoretical
  developments that show promise of resolving the current crisis by
  bridging the gap between theory and experiment. This is the aim
  of Part III.
• To discuss some sociological issues in contemporary academic
  science which I argue are slowing the progress of science, and to
  propose solutions to them. This is the aim of Part IV.

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.

The issue of the lack of predictability due to the landscape of solutions.
The need for-and lack of-a manifestly background independent formulation.
The frustrating situation that despite much very good work we
still don’t have a proof of key conjectures including
perturbative finiteness, S duality and the Maldacena conjecture.

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.

Response to review of The Trouble with Physics by Joe Polchinski

Lee Smolin, April 2007

A number of people have asked me to reply to a review of The Trouble with Physics by Joe Polchinski. I had been hesitant to because it is generally considered rude for an author to reply to a review-the author has had his or her say and so has the reviewer; any one who wants to can compare them and decide who to believe. The only exception is if the review misquotes or grossly misrepresents the book, but this was not one of those cases. Polchinski’s review was one of those that treated my and Peter Woit’s books respectfully and replied with a discussion of the evidence, without indulging in ad hominum attacks or misrepresentations. Given this, I felt no need to respond.

However, a number of people have commented on blogs or said to me directly that the lack of a response to Polchinski’s review was being taken as a concession on my part that I agreed with his criticisms of my book. Given this, I have concluded that it would not be inappropriate to make a few remarks in reply to what I understand to be factual disagreements. Beyond these there are of course matters of differing scientific judgments about open problems. However, a major point of my book is that such disagreements are to be respected as necessary for the progress of science, so I certainly have no need or desire to take issue with Polchinski on these points.

Polchinski begins, perhaps inadvertently, with one of the most perceptive remarks made by a reviewer of TTWP: “Smolin presents the rise and fall of string theory as a morality play.” I thank him for this, as he correctly sees that the key idea of the book is that the success of science is due to the formation of communities tied together by adherence to ethical principles. This ethical communities theory of what science is and how it works is, to my mind, the major theme of the book and its presentation, in Chapter 17, is the key to reading the book. As Polchinski perceives, the story of string theory serves this theme as a case study.

With regard to these broader issues, Polchinski thinks that Woit and I exaggerated the sociological issues, “such influences are not as strong as these authors posit…” Very sadly, I have to say that my impression is that some of the response to the books show the opposite. In the book I raised the idea of “groupthink” and then explained why I did not think it applied completely to the string community. But I have had to revise my views as the responses of a few string theorists, such as at George Johnson’s seminars at KITP, and certain online critiques and debates, offered textbook examples of groupthink. Rather than regarding criticism as an opportunity for reflection and response, colleagues in these settings were driven to demonize us, calling us cranks and worse, questioning our integrity and motives, while proudly insisting on not reading the books. These unfortunate responses gave a very unflattering portrait of our community, its openness to criticism from experts and its welcoming of a diversity of approaches.

Of course I have been very gratified that the vast majority of string theorists I have encountered or communicated with since TTWP was published have been friendly and, if the book came up, respectful and, in some cases even supportive and complementary. Also not surpringly, a few have expressed their disagreements, in some cases strong, with the content of the book, and when there was interest this led to an exchange of views, always friendly and professional.

Now onto some of the scientific issues:

Polchinski raises the issue of a positive cosmological constant and says my treatment of it is “based on a myth” In his words: ‘Smolin claims that string theorists had predicted that the energy of the vacuum — something often called dark energy — could not be positive and that the surprising 1998 discovery of the accelerating expansion of the universe (which implies the existence of positive dark energy) caused a hasty retreat. There was, in fact, no such prediction. Although his book is for the most part thoroughly referenced, Smolin cites no source on this point.”

Now, here is what I say, and please note the careful wording, “One of the few things we could conclude from the string theories then known was that the cosmological constant could only be zero or negative. I don’t know of any particular string theorist who predicted that the cosmological constant could not be a positive number, but it was widely understood to be a consequence of string theory. The reasons are too technical to do justice to them here.’ p 153. Please note the qualification “then known”-and note that I explain why there is no citation.

For experts, let me mention the technical argument I had in mind. It begins with the fact that supersymmetry requires that the cosmological constant be zero or negative. Supersymmetry, however, appears necessary in perturbative string theories to cancel the tachyonic instabilities. Now there has been some work that suggests that these may cancel at least to leading order with a weaker condition like Fermi-boson mass matching- but to my knowledge, there is no demonstration of consistent perturbative string theory without some such condition. This remains true even more than 3 years after the KKLT-which only gave evidence for string theories with positive cosmological constant at the semi-classical level. Indeed, we still have no evidence for any of these theories past the semi-classical level so it is in fact still an open problem whether there are any consistent string theories on positive cosmological constant backgrounds.

I did quote Witten saying, “I don’t know any clear-cut way to get de Sitter space from string theory or M-theory. This last statement is not very surprising given the classical no go theorem. For, in view of the usual problems in stabilizing moduli, it is hard to get de Sitter space in a reliable fashion at the quantum level given that it does not arise classically.” E. Witten, “Quantum Gravity in de Sitter Space,” hep-th/0106109.

Polchinski asserts that this was addressed to another context; if he has reason to believe this he ought to explain it, as Witten’s paper-which is highly interesting-seems to read pretty straightforwardly.

Polchinski goes on in his notes to assert “It is obvious that there could have been no such prediction. From 1995-98, string theorists were discovering a host of new nonperturbative tools: dualities, branes, black hole entropy counting, matrix theory, and AdS/CFT duality. These were at the time studied almost exclusively in the context of supersymmetry. The problem of moduli stabilization, necessary for any nonsupersymmetric compactification (and positive energy density states are necessarily nonsupersymmetric) was left for the future; there were no general results or predictions.”

If Polchinksi says that he and other string theorists were not concerned because they believed that the problem of moduli stabilization would eventually-when studied-lead to a theory with positive cosmological constant, I cannot disagree. But I can report that other people I spoke with were worried. Not the least because the problem of moduli stabilization was unsolved and known to be difficult.

It is indeed, characteristic of the style of research I criticize in TTWP, that a difficult problem whose solution was absolutely necessary to the success of string theory as a physical theory-moduli stabilization-could be happily left for the future. I do not recall any string theory talk or paper stating “string theory will be an interesting candidate for a physical theory if the very difficult problem of moduli stabilization can be successfully solved.” But this is what they ought to have said, (here is my ethics coming in here) had they given a true account of the situation.

At present we have evidence that the problem can be solved, at least at the semi-classical level. All the discussions that rely on the KKLT and related mechanisms assume that a still more difficult problem can be solved, which is to develop a fully stable, consistent and finite perturbation theory around the semi-classical vacua which have been stabilized.

If moduli stabilization and the problem of making a positive cosmological constant string theory were not seen as crises among the people Joe talks with, this seems to me just to confirm that they work in a closed intellectual universe in which an optimistic slant is put on everything and hopes are confused with results. But from the point of view of others there was a big problem. I recall many discussions about the difficulty string theory faced accounting for the observations of positive dark energy. At this time I was working on a series of results on LQG with positive cosmological constant. At some of the talks I gave on these results the issue of whether string theory could do the same came up and no one ever disagreed with my assertion that this was a problem.

Regarding the Ads/CFT conjecture, let me first emphasize that no claim in my book is contradicted by what Polchinksi says here. I stated that there is lots of evidence for some form of the AdS/CFT conjecture. And I am not surprised that evidence has continued to accumulate since the book was finished. What I questioned in the book-and continue to question-is that there is proof for the strongest form of the conjecture, which posits an exact equivalence between string theory on AdS5 x S5 and N=4 SYM. There are two points here, The first is that evidence is not proof, and for there to be a proof of equivalence between two mathematical objects each must be well defined. You cannot prove X is isomorphic to Y without having explicit definitions of X, Y and the isomorphism. There is no rigorous non-perturbative definition of “string theory on an asymptotically AdS5 x S5 background”, and there is no rigorous non-perturbative definition of N=4 SYM in d=4. Without them we cannot be sure that there are even well defined mathematical structures that correspond to these words.

The second point is that a weaker form of the conjecture might be true. Indeed, this must be the case given what we have just said about the lack of a complete non-perturbative formulation of either objects of the conjecture. What is at issue is whether in addition the strong form postulated by Maldacena is true.

Regarding background independence, Polchinski claims that, “(as Smolin belatedly notes), Maldacena duality provides a solution to this problem, one that is unexpected and powerful.” This exaggerates and distorts the situation. What is true-and what I acknowledge, is that if the strong form of the AdS/CFT conjecture is shown to be correct, then a very weak, and limited form of background will have been achieved. But for reasons just mentioned, which I explain in detail in the book, this is still a big if.

What has been shown so far relies on the fact that one can use the fact that SUSY N=4 Yang-Mills has the same global super-symmetry as perturbative physics on a background AdS5 X S5 spacetime, to express some physical quantities in the latter in terms of observables of the former. This is great mathematical physics and a great achievement, but the whole point of general relativity and quantum gravity is that the generic solutions are governed by no global symmetries because the geometry of spacetime is completely dynamical. This has two implications. First it makes it very non-trivial to show the strong form of the Maldacena conjecture, because it must extend to solutions of supergravity arbitrarily far from those with global symmetries in the bulk. However, if this is possible at all it will be because the full algebra of global super-symmetries remain on the boundary. The case of asymptotically flat will be much harder because there the asymptotic symmetries of the generic case are very different from the global symmetries of the ground state, and indeed there are no proposals for a gauge-gravity duality in this case. The case of positive cosmological constant-which appears to be the physical case-is harder still. And we have not even yet touched the real meaning of background independence, which is that fixed classical fields or global symmetries play absolutely no role in the formulation of the dynamics or observables of the theory.

The latter is what is meant by background independence in the rest of the classical and quantum gravity world, and so far string theory and the AdS/CFT conjectures do not come close to addressing it. It was in fairness to string theory that I was willing to acknowledge that the strong form of the AdS/CFT conjecture, if true, would provide a very limited and weak form of background independence. One would hope that in fairness to the truth string theorists who make this point would also hasten to acknowledge how far this would be from the real, full meaning of background independence. Brian Greene does acknowledge this when he proposes that the latter idea be distinguished by calling it “manifest background independence.”

Polchinski also acknowledges the difference, when he says, “In string theory it has always been clear that the physics is background-independent even if the language being used is not, and the search for a more suitable language continues.” But this is not the most accurate way to put it. It would be more accurate to say, “Some string theorists believe that the formulations of perturbative string theories and dualities between them that they study concretely are approximations to a deeper, background independent formulation. This missing background independent formulation is not just a different t language for the theory, it is hoped to be the statement of the principles and laws that define the theory, from which everything studied so far would be derived as an approximation. Despite this belief, only a few concrete proposals have been made for the laws and principles of this conjectural background independent formulation of string theory and none has gained wide support.”

The difference between how Polchinski puts it and I put it are I think indicative of some of the issues TTWP raises about over-statements of results.

Following this, Polchinski goes further and says something that seems just false, “But his principal candidate (loop quantum gravity) is, as yet, much more background-dependent than the current form of string theory.” In a note he explains this as “I am referring here to the problem of the constraints. Until these are solved, one does not really have background independence: there is an enormous Hilbert space, most of which is unphysical.” This is confusing and misleading, for two reasons. First we have the exact and general solution to the spatial diffeomorphism constraints. We also have-with certain choices of orderings of the Hamiltonian constraint-several infinite classes of solutions to all the constraints. We also have many versions of dynamical quantum geometries in which all the constraints are satisfied. So I don’t know what “until these are solved” could refer to. Second, the enormous Hilbert space he refers to is a consequence of the background independence, it is enormous because it permits all possible backgrounds. By now it is well understood that this expansion of the Hilbert space is a necessary step to constructing a subspace of states invariant under the exact diffeomorphisms.

The best interpretation I can put on this remark is that Polchinski is ignorant of basic and well established results of LQG. That such a good scientist could appear to be so ignorant of the basic results of a major research program rival to his own is part of the problem the title of my book refers to.

On the role of mathematics, Polchinski asserts that “Much of Smolin’s criticism of string theory deals with its lack of mathematical rigor. But physics is not mathematics. Physicists work by calculation, physical reasoning, modeling and cross-checking more than by proof, and what they can understand is generally much greater than what can be rigorously demonstrated.” Certainly, but the point is that the missing elements and demonstrations are not missing only at a rigorous level. Even at a physicists non-rigorous level we have no proof of perturbative finiteness, S-duality, the existence of perturbative string theories with positive cc backgrounds, or the strong form of the Maldacena conjecture. And, as many string theorists have noted, we have no statement of the principles of the theory and no succinct set of equations, analogous to the Einstein or Schroedinger equations that define the theory. This is not a matter of rigor.

It is also false that there are no mathematically rigorous results in physics. There are lots of rigorous results and theorems in classical general relativity, classical mechanics, quantum mechanics and statistical mechanics. There are even a number in quantum field theory. There are also rigorous results in LQG. It is true that it has so far proved impossible to rigorously define the standard model, but that may be because that theory does not exist. From this point of view, the lack of rigorous results in a well studied subject can be taken as evidence that the approximate methods used do not define a real theory-because, I would hope everyone would agree that any real physical theory must sooner or later admit a formulation in terms of rigorous mathematics.

With regard to heavy ion physics, yes the applications of the AdS/CFT duality to this are interesting and important. But they should not be exaggerated. Polchinski does so when he says, “And so the quantum gravity that is manifesting itself in dual form at Brookhaven is likely to be the same one that operates everywhere else in the universe.” First because there is no quantum gravity here, in this particular application only the correspondence with classical supergravity arises. Second, what is the basis for the “likely” here? I can imagine an aether theorist making the same argument: aether theory must be right because after a lot of work the principle of relativity of inertial frames was shown to be a consequence of the dynamics of the aether, therefore since nature “uses a small number of principles in diverse ways”, the aether must be the right explanation for why this principle is observed in nature. Further, it remains the case that the calculations behind these claims are done with an extended super-symmetric theory, when real QCD has no super-symmetries at all. It may be that they get some things approximately right for reasons that have nothing to do with string theory, such as the use of a scale invariant theory to provide a rough approximation of a non-scale invariant theory, in an experimental regime which has approximate scaling.

On cosmological application of string theory: “A further development over the past few years, as our understanding has deepened, has been the extensive study of the experimental consequences of specific kinds of string theory. Many of these make distinctive predictions for particle physics and cosmology. Most or all of these may well be falsified by experiment (which is, after all, the fate of most new models). The conclusive test of string theory may still be far off, but in the meantime, science proceeds through many small steps.” Given the infinite number of string theories, most with a large number of free parameters, it is not surprising that some can be found that predict phenomena that, with appropriate adjustments of free parameters, put some effects just at the threshold of observability. This is just a consequence of the lack of falsifiability of the theory. Of course, if some new phenomena were discovered experimentally that could only be explained on the assumption that string theory is the fundamental theory of nature, that would be all the proof that is needed. But in most of these cases, such as cosmic strings, there are already on the table alternative explanations for such effects which do not involve fundamental string theory.

Polchinski’s piece is a spirited defense of string theory and, in particular, of the view that the right thing to do in the face of the issues Woit as I raise is to continue to follow the theory for what may be a very long time into the future, given that he agrees that “conclusive test of string theory may still be far off.” Of course, the key point on which good scientists differ in their judgments is precisely how long is too long to invest a large portion of our resources in fundamental theory on such a long and risky bet.

This is fine so far as it goes, but nonetheless in retrospect it is disappointing that Polchinski has chosen to not engage with the broader arguments of the book. The reason why string theory occupies one of four parts of the book was to give a context in which to raise some broad and fundamental questions about how science works, and how well it works in the present academic environment-compared to earlier times when there were many fewer scientists, they were far less organized and professionalized and yet, progress was faster. The issues that Polchinski chooses not to deal with include:

-Unification through higher dimensions is an old idea, going back to 1914. It failed over and over again, for reasons that are key to the issues string theory now faces-stabilization of compactifications and the vast freedom of choices for the higher dimensional geometry and topology. Thus, what is in trouble now is not just string theory, it is an almost century old idea which suffers those two fatal flaws.

-The present situation is anomalous in the light of history. Almost always, when the right idea or explanation was put on the table it succeeded quickly to make contact with experiment. In some cases the new theory inspired new proposals for experimental tests that within a decade confirmed the new theory’s predictions.

(Polchinski alludes to atomism as a counter-example, but it is not much of one. There is a difference between a general philosophical idea-that the world is made of atoms-and a detailed theory-such as the Rutherford, Bohr or Schroedinger atoms. My discussion concerns theories, and indeed these theories of the structure of the atom found experimental support immediately. If one wants to say that there is a general idea that the true degrees of freedom in nature are extended objects then that is fine, but that general idea does not distinguish string theory from loop quantum gravity and spin foam models.)

My hope in writing this book was not to “kill” string theory, and indeed I emphasize that string theory is among the ideas I believe are worth still exploring, in the context of a lively, diverse and critical environment in which different ideas compete to prove themselves. What I did hope to do was to kill thc complacent “only game in town”, groupthink attitude towards string theory-which I argue in the book was held for reasons that are both factually false and inimical to the progress of science. By doing so I hoped to bring about a lively, open minded debate within the field in which we all asked ourselves how it could happen that our best and brightest would seize on an apparently unique theory that turned out decades later to have still no complete and coherent formulation and to come in an apparent infinite number of versions and so make no falsifiable predictions. What I hoped for was a detailed debate on the scientific and sociological issues, which took the current situation, not as a public relations crisis for one research program, but as a genuine intellectual puzzle and challenge to all of us who hope to contribute to the progress of physics.

I did this because I thought and still think such a debate would be good for progress. Among other reasons, because it would open up the field to new and better ideas by people not committed already to a single research program. Polchinski’s review is so far the best public response from a string theorist to my book, but it falls far short of taking on the real debate and issues raised in the book. Perhaps there will be soon miraculous developments that will render such a debate unnecessary, but in their absence I, and the many colleagues who havc responded very positively to my book, stand ready to have it.