# February 25, 2007 {#week246}

I've been gearing up to tell a big, wonderful story about the quest to
generalize quantum knot invariants to higher dimensions by categorifying
the theory of quantum groups. This story began at least 14 years ago! I
talked about it way back in ["Week 2"](#week2).

At the time, Louis Crane and Igor Frenkel had just come out with a draft
of a paper called "Hopf categories and their representations", which
began tackling this problem. This is roughly when Crane invented the
word "categorification" --- and their paper is a big part of why I got
interested in $n$-categories.

The subject moved rather slowly until Frenkel's student Mikhail
Khovanov got into the game and categorified the Jones polynomial --- a
famous invariant of knots related to the very simplest quantum group,
the one called "quantum $\mathrm{SU}(2)$". Now categorifying knot theory is a hot
topic.

James Dolan, Todd Trimble and I have been chewing away on this subject
from a quite different angle, which may ultimately turn out to be the
same --- or at least related. In the process, we've needed to learn,
reinvent or remodel a lot of classical work on group theory, incidence
geometry, and combinatorics. It's been a great adventure, and it's far
from over.

I'm dying to explain some of this stuff, and I'll start soon. But
first I need to talk about something less pleasant: the troubles with
fundamental physics.

If you care at all about physics, you've probably heard about these:

1) Peter Woit, _Not Even Wrong: The Failure of String Theory and the Continuing Challenge to Unify the Laws of Physics_, Basic Books, New York, 2006.

2) Lee Smolin, _The Trouble With Physics: The Rise of String Theory, the Fall of a Science, and What Comes Next_, Houghton Mifflin, New York, 2006.

I won't "review" these books. I'll just talk about some points they
raise --- in a very nontechnical way.

Their importance is that they explain the problems of string theory to
the large audience of people who get their news about fundamental
physics from magazines and popular books. Experts were already aware of
these problems, but in the popular media there's always been a lot of
hype, which painted a much rosier picture. So, casual observers must
have gotten the impression that physics was always on the brink of a
Theory of Everything... but mysteriously never reaching it. These books
correct that impression.

In fact, string theory still hasn't reached the stage of making any
firm predictions. For the last few decades, astrophysicists have been
making amazing discoveries in fundamental physics: dark matter, dark
energy, neutrino oscillations, maybe even cosmic inflation in the very
early universe! Soon the Large Hadron Collider will smash particles
against each other hard enough to see the Higgs boson --- or not. With
luck, it may even see brand new particles. But about all this, string
theory has had little to say.

To get actual predictions, practical physicists sometimes build
"string-inspired" scenarios. These scenarios aren't *derived* from
string theory: to get specific predictions, they have to throw in lots
of extra assumptions. For example, since string theory involves
supersymmetry, string theorists resort to supersymmetric versions of the
Standard Model to guess what the Large Hadron Collider might see. But
the simplest supersymmetric version of the Standard Model involves over
100 undetermined parameters! Even the particles we actually see are put
in by hand, not derived from string theory. If it turns out we see some
other particles, we can just stick those in too.

Someday this situation may change, but it's dragged on for a while now.
There's no reason why theoretical physics should always move fast. The
universe has taken almost 14 billion years to reach its current state of
self-knowledge --- what's a few more decades? But, coming after an era of
incredibly rapid progress stretching from 1905 to 1983, the current
period of stagnation feels like an eternity. So, physicists are getting
a bit desperate. This has led to some strange behavior.

For example, some people have tried to refute the claim that string
theory makes no testable predictions by arguing that it predicts the
existence of gravity! This is better known as a "retrodiction".

Others say that since string theory requires extra assumptions to make
definite predictions about our universe, we should --- instead of making
some assumptions and using them to predict something --- study the space
of *all possible* extra assumptions. For example, there are lots of
Calabi-Yau manifolds that could serve as the little curled-up dimensions
of spacetime, and lots of ways we could stick D-branes here or there,
etcetera.

This space of all possible extra assumptions is called the
"Landscape". Since it's vaguely defined, the main things we know
about it are:

a) it's big,
b) it keeps growing as string theorists come up with new ideas,
c) nobody has yet found a point in it that matches our universe.

Despite this, or perhaps because of it, the Landscape has been the
subject of many discussions. Often these devolve into arguments about
the "anthropic principle". Roughly, this says that if the universe
were really different, we wouldn't be having this argument --- so it must
be like it is!

One can in fact draw some conclusions from the anthropic principle. But
it's really just the low-budget limit of experimental physics. You can
always get more conclusions from doing more experiments. The experiment
where you just check to see if you're alive is really cheap --- but you
don't learn much from it.

(Of course I'm oversimplifying things for comic effect, but usually
people take the opposite approach, overcomplicating this stuff to make
it sound more profound than it is.)

Serious string theorists are mostly able to work around this tomfoolery,
but it exerts a demoralizing effect. So, when Woit and Smolin came out
with their books, a lot of tempers snapped, and a lot of strange
arguments were applied against them.

For example, one popular argument was "Okay, buster --- can you do
better?" The idea here seems to be that until you know a solution to
the problems faced by string theory, you shouldn't point out these
problems --- at least not publicly. This goes against my experience: hard
problems tend to get solved only *after* lots of people openly admit
they exist.

Another closely related argument was "String theory is the only game in
town." Until some obviously better theory shows up, we should keep
working on string theory.

It's true there's no obviously better theory than string theory. Loop
quantum gravity, in particular, has problems that are just as serious as
string theory.

But, the "only game in town" argument is still flawed.

Once I drove through Las Vegas, where there really *is* just one game in
town: gambling. I stopped and took a look. I saw the big fancy casinos.
I saw the glazed-eyed grannies feeding quarters into slot machines,
hoping to strike it rich someday. It was clear: the odds were stacked
against me. But, I didn't respond by saying "Oh well --- it's the only
game in town" and starting to play.

Instead, I *left* that town.

It's no good to work on string theory with a glum attitude like "it's
the only game in town." There are lots of other wonderful things for
theoretical physicists to do. Things where your work has a good chance
of matching experiment... or things where you take a huge risk by going
out on your own and trying something new.

Indeed, if following the crowd were the name of the game, string theory
might never have been invented in the first place. It didn't fall from
the sky fully formed, obviously better than its competitors. A handful
of people took a big chance by working on it for many years before it
proved its worth.

In his book, Lee Smolin argues that physics is in the midst of a
scientific revolution, and that these times demand people who don't
just follow fashion:

> The point is that different kinds of people are important in normal
> and revolutionary science. In the normal periods, you need only people
> who, regardless of their degree of imagination (which may well be
> high), are really good at working with the technical tools --- let us
> call them master craftspeople. During revolutionary periods, you need
> seers, who can peer ahead into the darkness.

He later regretted this way of putting it, and I think rightly so. The
term "seer" suggests that some people have a better-than-average
ability to see the right answers to profound questions. This may be
true, but it's hard to tell ahead of time who is a seer and who is not.
Smolin later wrote:

> Here is a metaphor due to Eric Weinstein that I would have put in the
> book had I heard it before. Let us take a different twist on the
> landscape of theories and consider the landscape of possible ideas
> about post standard model or quantum gravity physics that have been
> proposed. Height is proportional to the number of things the theory
> gets right. Since we dont have a convincing case for the right theory
> yet, that is a high peak somewhere off in the distance. The existing
> approaches are hills of various heights that may or may not be
> connected across some ridges and high valleys to the real peak. We
> assume the landscape is covered by fog so we cant see where the real
> peak is, we can only feel around and detect slopes and local maxima.
>
> Now to a rough approximation, there are two kinds of scientists --- hill
> climbers and valley crossers. Hill climbers are great technically and
> will always advance an approach incrementally. They are what you want
> once an approach has been defined, i.e. a hill has been discovered,
> and they will always go uphill and find the nearest local maximum.
> Valley crossers are perhaps not so good at those skills, but they have
> great intuition, a lot of serendipity, the ability to find hidden
> assumptions and look at familiar topics new ways, and so are able to
> wander around in the valleys, or cross exposed ridges, to find new
> hills and mountains.
>
> I used craftspeople vs. seers for this distinction, Kuhn referred to
> normal science vs. revolutionary science, but the idea was the same.
>
> With the scene set, here is my critique. First, to progress, science
> needs a mix of hill climbers and valley crossers. The balance needed
> at any one time depends on the problem. The more foundational and
> risky a problem is the more the balance needs to be shifted towards
> valley crossers. If the landscape is too rugged, with too many local
> maxima, and there are too many hill climbers vs. valley crossers, you
> will end up with a lot of hill climbers camped out on the tops of
> hills, each group defending their hills, with not enough valley
> crossers to cross those perilous ridges and swampy valleys to find the
> real mountain.
>
> This is what I believe is the situation we are in. And --- and this is
> the point of Part IV \[of the book\] --- we are in it, because science
> has become professionalized in a way that takes the characteristics of
> a good hill climber as representative of what is a good, or promising
> scientist. The valley crossers we need have been excluded, or pushed
> to the margins where they are not supported or paid much attention to.
>
> My claim is then 1) we need to shift the balance to include more
> valley crossers, and 2) this is easy to do, if we want to do it,
> because there also are criteria that can allow us to pick out who is
> worthy of support. They are just different criteria.

This is a good analysis, but it leaves out one thing: most "valley
crossers" get stuck wandering around in valleys. Even those who succeed
once are likely to fail later: think of Einstein's long search for a
unified field theory, or Schrödinger's "unitary field theory"
involving a connection with torsion, or Heisenberg's nonlinear spinor
field theory, or Kelvin's vortex atoms. It's not surprising these
geniuses spent a lot of time on failed theories --- what's surprising is
their successes.

So, failure is an unavoidable cost of doing business, and encouraging
more "valley crossers" or "risk takers" will inevitably look like
encouraging more failures.

Unfortunately, the alternative is even more risky. If everyone pursues
the same approach, we'll all succeed or fail together --- and chances are
we'll fail. The reason for backing some risk takers is that it
"diversifies our portfolio". It reduces overall risk by increasing the
chance that *someone* will succeed.

(It's no coincidence that Eric Weinstein, mentioned above by Smolin,
works as an investment banker. He's also a student of Raoul Bott --- but
that's another story!)

Near the end of his book, Woit quotes the mathematican Michael Atiyah,
who also seems to raise the possibility that we need some more
risk-taking:

> If we end up with a coherent and consistent unified theory of the
> universe, involving extremely complicated mathematics, do we believe
> that this represents "reality"? Do we believe that the laws of
> nature are laid down using the elaborate algebraic machinery that is
> now emerging in string theory? Or is it possible that nature's laws
> are much deeper, simple yet subtle, and that the mathematical
> description we use is simply the best we can do with the tools we
> have? In other words, perhaps we have not yet found the right language
> or framework to see the ultimate simplicity of nature.

Most people who read these words and try to find this "right
framework" will fail. But, we can hope that someday a few succeed.

For the fascinating tale of Schrödinger's "unitary field theory", see
this nice book:

3) Walter Moore, _Schrödinger: His Life and Thought_, Cambridge U. Press, Cambridge, 1989.

For more about the search for unified field theories in early 20th
century, see:

4) Hubert F. M Goenner, "On the history of unified field theories", _Living Reviews of Relativity_ **7**, (2004), 2. Available at `http://www.livingreviews.org/lrr-2004-2`

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**Addenda:** I thank Eugenia Cheng and Eugene Lerman for catching
mistakes. For more discussion, go to the
[$n$-Category Café](http://golem.ph.utexas.edu/category/2007/02/this_weeks_finds_in_mathematic_7.html).

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> *Apart from agreeing with reality it is certainly a magnificent
achievement of pure thought.*
> 
> --- Einstein, to Hermann Weyl, about Weyl's attempt to unify gravity and electromagnetism.