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

  1. Feb 26, 2007 #1
    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 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

    -----------------------------------------------------------------------
    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
     
  2. jcsd
  3. Feb 26, 2007 #2
    The problem with fundamental physics is pride, and I'm not even mildly convinced that a complete contradiction to the standard model at the higgs scale will do anything to shake the false confidence in assumptions and other ad hoc that dates farther back than anybody is willing to swallow their pride for.

    Why the heck would you want to push for new maths that will no doubt also only serve to advance the absurdity an existing problem that must surely exist at least thirty years in the past, if you are correct when you say that fundamental (theoretical) physics hasn't advanced since then?

    I think it'll be something we've all missed!

    Except that nobody really believes this.

    Lee Smolin says a lot of similarly "good stuff" that he also only very conditionally believes.

    That's the real problem with fundamental physics.
     
  4. Feb 28, 2007 #3
    In article <ert5tc$4og$2@glue.ucr.edu>,
    baez@math.removethis.ucr.andthis.edu (John Baez)
    wrote:

    > 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.


    How did the popular media convey impression? Why could
    not the popular media have corrected this impression
    all along? Why did not the physicists involved soft
    peddle string theory. It is too late now to say
    everybody got the wrong impression for twenty-five
    years. Physics shot itself in the foot.

    --
    Michael Press
     
  5. Mar 1, 2007 #4
    Michael Press wrote:
    > In article <ert5tc$4og$2@glue.ucr.edu>,
    > baez@math.removethis.ucr.andthis.edu (John Baez)
    > wrote:
    >
    >> 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.

    >
    > How did the popular media convey impression? Why could
    > not the popular media have corrected this impression
    > all along? Why did not the physicists involved soft
    > peddle string theory. It is too late now to say
    > everybody got the wrong impression for twenty-five
    > years. Physics shot itself in the foot.


    Probably, but now there is an abundance of new experimental data to work
    with, most notably the supposed Dark Matter and esp Dark Energy. I
    suspect they may be the equivalent of the Michaelson Morley expt in
    their significance and dissonance with existing theory.

    --
    Dirk
     
  6. Mar 24, 2007 #5
    In article <rubrum-C8B1CE.21420126022007@newsclstr02.news.prodigy.com>,
    Michael Press <rubrum@pacbell.net> wrote:

    >In article <ert5tc$4og$2@glue.ucr.edu>,
    > baez@math.removethis.ucr.andthis.edu (John Baez)


    >> 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.


    >How did the popular media convey [this] impression?


    Popular articles about physics over the last few decades keep
    talking about the wonderful ideas string theorists are coming up with
    and rarely point out that these ideas aren't testable (at least not
    yet). To see what I mean, try this:

    Peter Woit
    Is String Theory Testable?
    http://www.math.columbia.edu/~woit/testable.pdf

    Look at the articles in the popular media, and then read Woit's
    remarks.

    Or even better, read Woit's book! And Smolin's!

    >Why could not the popular media have corrected this impression
    >all along?


    They could have. However, the popular media like exciting stories,
    and there are plenty of string theorists willing to give them exciting
    stories.

    >Why did not the physicists involved soft peddle string theory?


    Because soft peddling your ideas doesn't make you famous, and
    there wasn't enough social pressure on them to be cautious.

    In particular, the newspapers don't often publish stories saying
    "Remember Prof. X's far-out theory from last year? Well, it's wrong."
     
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