- #1
John Baez
Also available as http://math.ucr.edu/home/baez/week246.html
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 anyone 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
-----------------------------------------------------------------------
Previous issues of "This Week's Finds" and other expository articles on
mathematics and physics, as well as some of my research papers, can be
obtained at
http://math.ucr.edu/home/baez/
For a table of contents of all the issues of This Week's Finds, try
http://math.ucr.edu/home/baez/twfcontents.html
A simple jumping-off point to the old issues is available at
http://math.ucr.edu/home/baez/twfshort.html
If you just want the latest issue, go to
http://math.ucr.edu/home/baez/this.week.html
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 anyone 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
-----------------------------------------------------------------------
Previous issues of "This Week's Finds" and other expository articles on
mathematics and physics, as well as some of my research papers, can be
obtained at
http://math.ucr.edu/home/baez/
For a table of contents of all the issues of This Week's Finds, try
http://math.ucr.edu/home/baez/twfcontents.html
A simple jumping-off point to the old issues is available at
http://math.ucr.edu/home/baez/twfshort.html
If you just want the latest issue, go to
http://math.ucr.edu/home/baez/this.week.html