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February 24, 2007

This Week's Finds in Mathematical Physics (Week 246)

John Baez

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 "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 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 wonderful 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, Jonathan Cape,

London, 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 wonderful 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, one has to throw in lots of

extra assumptions. For example, since string theory involves

supersymmetry, physicists have built 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, and 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.

In short, 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 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 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 don’t 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 can’t 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 Schroedinger'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 Isadore Singer

and a big fan of Bott periodicity - 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 Schroedinger's "unitary field theory", see

this wonderful book:

3) Walter Moore, Schroedinger: 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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# This Week's Finds in Mathematical Physics (Week 246)

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