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 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 donít 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 canít see where the real peak is, we can only feel around and detect slopes and local maxima.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.
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.
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
Addenda: I thank Eugenia Cheng and Eugene Lerman for catching mistakes. For more discussion, go to the n-Category Café.
© 2007 John Baez