Science Fashions and Scientific Facts
Thomas Larsson
by Michael Riordan, of Stanford and Santa Cruz, entitled "Science
Fashions and Scientific Facts". This article can be found online at
http://www.aip.org/pt/vol-56/iss-8/p50.html
Here are some key quotes:
Page 51, top left:
"How can we ever hope to work in everyday practice with such entities
as superstrings, parallel universes, wormholes, and phenomena that
occurred before the Big Bang?
Some of these ideas may have great mathematical beauty and
significant explanatory power, but so did many discarded physics
fashions of the 1960s."
Page 51, middle:
"some people have even begun to suggest that we relax our criteria
for establishing scientific fact. [...] According to a leading
science historian, such a subtle but ultimately sweeping
philosophical shift in theory justification may already be underway.
[...] Then there would be little to distinguish the practice of
physics from, say, that of painting or print-making. [...] The
primary criterion of good science must remain that it has been
repeatedly tested by measurements. [...]
Without such a rigorous standard of truth, science will have little
defence against the onslaughts of the creationists and
postmodernists. "
Personally, I find it extremely disturbing that most physics
professors, by their passivity, are allowing this paradigm shift to
occur.
John Baez
Thomas Larsson <thomas_l...@hotmail.com> wrote:
>Page 51, middle:
>
>"some people have even begun to suggest that we relax our criteria
>for establishing scientific fact. [...] According to a leading
>science historian, such a subtle but ultimately sweeping
>philosophical shift in theory justification may already be underway.
Who is this mysterious unnamed "leading science historian"?
>Without such a rigorous standard of truth, science will have little
>defence against the onslaughts of the creationists and
>postmodernists. "
I believe that high-energy particle physics has entered a
somewhat decadent phase where less emphasis is being placed
on either matching the results of experiments *or* mathematical
rigor. It's becoming a bit like playing tennis with the nets down.
However, I don't see this tiny branch of science as being
representative of science as a whole. When one reads a journal
like Science or Nature one is forcefully reminded that these days,
science is dominated by biology and its applications to medicine.
Here empiricism is still perfectly alive and well, despite a certain
amount of fraud due to the big bucks involved.
So, I think that this "leading science historian" and the author of
the article you quote are being overly alarmist.
However, I think we must *constantly* fight to prevent the
gradual rotting away of good scientific practice. To avoid
"truth decay", we must *always* emphasize the difference
between what we know, what we believe on the basis of pretty good
evidence, what we suspect on the basis of a little evidence,
what would be cool if it were true, what is fashionable this year,
etc.
Lubos Motl
> I believe that high-energy particle physics has entered a
> somewhat decadent phase where less emphasis is being placed
> on either matching the results of experiments *or* mathematical
> rigor. It's becoming a bit like playing tennis with the nets down.
Although I might also feel some reasons to call the very new era
"decadent", I totally disagree with the description of the reasons and
the symptoms.
Theoretical physics was never a part of mathematics, and the culture of
the physicists is different from the culture of the mathematicians.
Physicists simply do not want to write papers that are separated into
"axioms", "definitions", "theorems", and their "proofs" and "corollaries".
Theoretical particle physicists try to investigate the topics at the very
edge of our current understanding of the Universe. And this is a place
where the optimal mathematical formalism has not been settled yet - and it
usually takes a lot of time before the well-established theories are
translated into a strictly rigorous mathematical framework. Consequently,
it is usually counter-productive to insist on the mathematical rigor as
the mathematicians know it.
The physicists - unlike mathematicians - were always using "plausibility"
arguments that were not 100% certain, and it will be so until the
hypothetical discovery of the theory of everything. The reason why we
can't be quite 100% sure about something is that the object that we want
to understand is the real world that was created by God/Nature, and not a
system of mathematical axioms that are invented by the people. If you
invent your own axioms without the trial-and-error method to refine your
results and exclude the wrong conjectures, it is very likely that these
axioms won't apply to the real world. I think that many people should
re-read this favorite statement of Einstein's.
What is different about our era is that we are not aware of any
experiments that truly and clearly enough contradict our previous theory
of Nature - namely the pragmatic (but inconsistent) union of general
relativity (with the cosmological constant included) and the standard
model (with the neutrino masses included). We know that this "theory" is
good but not good enough, but we can only make progress without the new
experimental data. It is reasonable to expect that we won't have any solid
new data at least for 5 years.
This is a tough situation, but the theoretical physicists - I mostly mean
string theorists - are probably approaching this difficult situation in
the only reasonable way. They try to follow the methods that have worked
for centuries, but the (non-existing) experimental checks must be replaced
by some "other" type of quasi-theoretical checks. Fortunately, the
mathematical consistency plays a very important role for theories of
quantum gravity.
Particle phenomenology is not a rigorous mathematical field either, and
because phenomenologists don't have any new radical experimental data
either, they must try new ideas and study their consequences
theoretically. The only methodical difference from string theory is that
they try to study the new phenomena "from the bottom" - trying to
investigate each possible new phenomenon that will be discovered in the
actual future of our civilization - while string theorists are more
impressed by the huge constraints of gravitational and other physics at
high energies, and they try to extrapolate their theory from the top to
the bottom and predict the new phenomena perhaps in a different order than
the order in which they will be observed. All non-experimental particle
physicists suffer from the same lack of new experimental results, and our
experimental fellows are trying hard to show us something really new and
exciting.
The nets simply and objectively ARE down, and if you try to put your own
nets, then you're playing the tennis not your own mathematical inventions
rather than with Nature!
The recently discovered pentiquark (u u d d sbar) with its 1530 GeV is
very nice, but we believe that it is a rather complicated object that IS
contained in QCD, and we think that there are other, more important
questions. We desperately need some really new data!
I think that despite this temporary separation from the experiments,
theoretical physics is certainly not becoming inherently separated from
the experiments. And we are trying to solve puzzles that are bigger than
all puzzles in the past - with the possible exception of the discovery of
quantum physics. The promises are great, and therefore many scientists
find it irresistable and they continue to study theoretical particle
physics. Others leave. This is how it works and science has its own
self-regulating mechanisms. But those who stay must choose their methods
that reflect the current abilities of physics to do experiments, and in
this scheme of thing, mathematical consistency plays a more important role
than it did in the past. I say "mathematical consistency" which is
something different than "formal mathematical rigor"!
> However, I don't see this tiny branch of science as being
> representative of science as a whole. When one reads a journal
> like Science or Nature one is forcefully reminded that these days,
OK, let me still view these journals as representatives of popular and
applied science, not pure science. More concretely, I don't think that a
particle physicist should be proud if his or her paper is published in one
of these journals.
Best wishes
Lubos
______________________________________________________________________________
E-mail: lu...@matfyz.cz fax: +1-617/496-0110 Web: http://lumo.matfyz.cz/
phone: work: +1-617/496-8199 home: +1-617/868-4487
^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^
Superstring/M-theory is the language in which God wrote the world.
Kevin A. Scaldeferri
>Personally, I find it extremely disturbing that most physics
>professors, by their passivity, are allowing this paradigm shift to
>occur.
I think you might be confusing numbers with volume. That is, there
are some quite prominent and vocal people who may be doing what you
say, but to claim that most physicists have decided to discard the need
for experimental verification (and verifiability) would be to ignore
the debates which actually take place within most physics departments.
Of course, the press is not invited to faculty meetings, but believe
me that there are many professors who resist this "paradigm shift".
--
======================================================================
Kevin Scaldeferri Calif. Institute of Technology
The INTJ's Prayer:
Lord keep me open to others' ideas, WRONG though they may be.
Peter Shor
Lubos Motl <mo...@feynman.harvard.edu> wrote:
> On Tue, 30 Sep 2003, John Baez wrote:
>
> > I believe that high-energy particle physics has entered a
> > somewhat decadent phase where less emphasis is being placed
> > on either matching the results of experiments *or* mathematical
> > rigor. It's becoming a bit like playing tennis with the nets down.
> Although I might also feel some reasons to call the very new era
> "decadent", I totally disagree with the description of the reasons and
> the symptoms.
I've found this discussion quite interesting. It seems to me that
theoretical high-energy physics is facing a situation that physics
hasn't faced for roughly a century. At the beginning of the last
century (at least according to some accounts I've read), a lot of
physicists thought that physics was mainly solved, with only a few
theoretical inconsistencies (such as the ultraviolet catastrophe).
These inconsistencies were actually hints that quantum mechanics and
relativity existed, which of course were both major revolutions. Now,
we're again in the situation that known theories can explain nearly
all experimental observations. The main problem with theoretical
physics today is that quantum field theory seems to be inconsistent
with general relativity, as evidenced by the black hole information
loss question. The question is whether this is an inconsistency that
can be resolved by pure thought (as Einstein virtually did with
gravity) or one that needs input from experiment (I don't see how
anybody could have come up with quantum mechanics without substantial
experimental input, and one of Michael Riordan's points was that quark
theory would never have been accepted if it hadn't had substantial
experimental substantiation). The string theorists are hoping that
the current situation is more like the first case of relativity, but
this may be based more on hope than on any real evidence.
I'm also worried about string theory becoming the accepted doctrine
without any experimental evidence, which means that alternative
theories (like loop quantum gravity or, even worse, something new that
somebody comes up with and that nobody has thought about before) may
get rejected without having undergone any real scrutiny. An
experience that leads me to believe this is happening is that I've
mentioned to two string theorists John Preskill's idea that the
dynamics of the universe may lose information (and so be nonunitary)
on the Planck scale, but that this information loss is covered up by a
natural quantum error correcting code. They both reassured me that
this couldn't possible happen, because we'd see the non-unitary
behavior at macroscopic scales. I think there's evidence that this
glib reassurance is unfounded in the papers about quantum error
correction by anyons
quant-ph/9707021, quant-ph/0206128, quant-ph/0306063
although I must admit that I have no idea about how to go about figuring
how this natural quantum error correction could actually fit together
gravity and QFT.
> Theoretical physics was never a part of mathematics, and the culture
> of the physicists is different from the culture of the
> mathematicians. Physicists simply do not want to write papers that
> are separated into "axioms", "definitions", "theorems", and their
> "proofs" and "corollaries". Theoretical particle physicists try to
> investigate the topics at the very edge of our current understanding
> of the Universe. And this is a place where the optimal mathematical
> formalism has not been settled yet - and it usually takes a lot of
> time before the well-established theories are translated into a
> strictly rigorous mathematical framework. Consequently, it is
> usually counter-productive to insist on the mathematical rigor as
> the mathematicians know it.
I don't know if anybody here is saying that theoretical physicists
should be held to mathematical rigor. However, for most of the
century physicists (even particle physicists) were held to the
possibly much more stringent standard of having to agree with
experiments. Now, there's no experiments available that aren't well
explained by the standard theories.
> The physicists - unlike mathematicians - were always using
> "plausibility" arguments that were not 100% certain, and it will be
> so until the hypothetical discovery of the theory of everything.
Won't it be so even after the hypothetical discovery of this theory?
> The reason why we can't be quite 100% sure about something is that
> the object that we want to understand is the real world that was
> created by God/Nature, and not a system of mathematical axioms that
> are invented by the people. If you invent your own axioms without
> the trial-and-error method to refine your results and exclude the
> wrong conjectures, it is very likely that these axioms won't apply
> to the real world. I think that many people should re-read this
> favorite statement of Einstein's.
Actually, that's not the way mathematics is done, either. Inventing
axioms usually leads to obscure and unimportant theories. The trick is
inventing the right axioms. But this belongs to a different
discussion.
What is this statement of Einstein's, anyway?
> What is different about our era is that we are not aware of any
> experiments that truly and clearly enough contradict our previous
> theory of Nature - namely the pragmatic (but inconsistent) union of
> general relativity (with the cosmological constant included) and the
> standard model (with the neutrino masses included). We know that
> this "theory" is good but not good enough, but we can only make
> progress without the new experimental data.
The question is whether it's possible to make progress without the
experimental data (but if the alternative is giving up and telling all
the physicists to work on something else, I agree that we have to try
to make progress without experiment).
> It is reasonable to expect that we won't have any solid
> new data at least for 5 years.
And I assume it's possible that there won't be any solid data
for much longer, if the Higgs particle is discoverd on schedule and
there's no evidence of any physics beyond the standard model.
> This is a tough situation, but the theoretical physicists - I mostly
> mean string theorists - are probably approaching this difficult
> situation in the only reasonable way. They try to follow the methods
> that have worked for centuries, but the (non-existing) experimental
> checks must be replaced by some "other" type of quasi-theoretical
> checks. Fortunately, the mathematical consistency plays a very
> important role for theories of quantum gravity.
Yes, but the consensus that the ultimate theory of the universe has to
a string theory seems to me dangerously premature. Could you try to
explain to us laymen why the fact that string theory predicts that the
world is ten-dimensional means that we shouldn't start looking for other
ways of finding a theory of quantum gravity that accomodate a 4-dimensional
world (which would indeed agree more with experiment :-) ...)?
> The nets simply and objectively ARE down, ...
That's the problem.
> The recently discovered pentiquark (u u d d sbar) with its 1530 GeV is
> very nice, but we believe that it is a rather complicated object that IS
> contained in QCD, and we think that there are other, more important
> questions. We desperately need some really new data!
>
> I think that despite this temporary separation from the experiments,
> theoretical physics is certainly not becoming inherently separated from
> the experiments. And we are trying to solve puzzles that are bigger than
> all puzzles in the past - with the possible exception of the discovery of
> quantum physics.
For which discovery, experiments were crucial.
> The promises are great, and therefore many scientists find it
> irresistable and they continue to study theoretical particle
> physics. Others leave. This is how it works and science has its own
> self-regulating mechanisms. But those who stay must choose their
> methods that reflect the current abilities of physics to do
> experiments, and in this scheme of thing, mathematical consistency
> plays a more important role than it did in the past. I say
> "mathematical consistency" which is something different than "formal
> mathematical rigor"!
> > However, I don't see this tiny branch of science as being
> > representative of science as a whole. When one reads a journal
> > like Science or Nature one is forcefully reminded that these days,
> OK, let me still view these journals as representatives of popular and
> applied science, not pure science. More concretely, I don't think that a
> particle physicist should be proud if his or her paper is published in one
> of these journals.
Science and Nature are two of the premier journals in biology, even if
they aren't the most prestigious place to publish physics or mathematics
articles. As John Baez says, we shouldn't forget that most of science
is still quite well connected with experiment.
Peter Shor
Thomas Larsson
ba...@galaxy.ucr.edu (John Baez) wrote in message
news:<blcdtg$l27$1...@glue.ucr.edu>...
> In article <24a23f36.0309...@posting.google.com>,
> Thomas Larsson <thomas_l...@hotmail.com> wrote:
> >Page 51, middle:
> >
> >"some people have even begun to suggest that we relax our criteria
> >for establishing scientific fact. [...] According to a leading
> >science historian, such a subtle but ultimately sweeping
> >philosophical shift in theory justification may already be underway.
> Who is this mysterious unnamed "leading science historian"?
I have no information beyond what was published in Physics Today.
> >Without such a rigorous standard of truth, science will have little
> >defence against the onslaughts of the creationists and
> >postmodernists. "
> I believe that high-energy particle physics has entered a
> somewhat decadent phase where less emphasis is being placed
> on either matching the results of experiments *or* mathematical
> rigor.
This must be the understatement of the year. I see basically no
respect neither for experimental results (null results on SUSY, a
positive cosmological constant rules out AdS), nor for key properties
of successful theories (e.g. diffeomorphism invariance in general
relativity), nor for mathematics, rigorous or not (where are the
mathematical principles underlying M-theory or the anthropic
principle?)
> However, I don't see this tiny branch of science as being
> representative of science as a whole. When one reads a journal like
> Science or Nature one is forcefully reminded that these days,
> science is dominated by biology and its applications to medicine.
> Here empiricism is still perfectly alive and well, despite a certain
> amount of fraud due to the big bucks involved.
Riordan is a particle physicist and this is mainly what he is
talking about, even if he also mentions Wolfram's book (and of course
I agree with him on that issue too). Other fields of science seem to
be alive and well, although there certainly are hypes in molecular
biology as well (ever heard of the P53 gene?).
Ralph Hartley
> John Baez wrote:
>>However, I don't see this tiny branch of science as being
>>representative of science as a whole. When one reads a journal
>>like Science or Nature one is forcefully reminded that these days,
> OK, let me still view these journals as representatives of popular and
> applied science, not pure science. More concretely, I don't think that a
> particle physicist should be proud if his or her paper is published in one
> of these journals.
Well, you don't have much chance of getting a paper accepted by a primary
journal like *Cell*, do you? :-)
This is the kind of thinking that gives physicists a bad name.
If you think what's happening in biology these days is not pure science,
you haven't been paying attention. Just because something has potential
applications doesn't make it applied, any more than the discovery of
nuclear fission was applied science because it lead the bomb. Understanding
the cell cycle is pure research, curing cancer would be applied, though one
may eventually lead to the other. In fact, most of the current work in
biology is pure science, and hasn't reached the "applied" part of the
pipeline at all yet. Expect to hear about it when it does :-).
Besides, when earlier in your post you say
> It is reasonable to expect that we won't have any solid
> new data at least for 5 years.
and
> The nets simply and objectively ARE down ...
doesn't that amount to an admission that (due to circumstances beyond your
control) *you* won't be able to do any *real* science for at least 5 years?
The best particle physicists can realistically expect to do now is to
prepare for the day when new data starts coming again, try to hasten that
day, and refrain from throwing stones.
You *can't* play tennis without a net, all you can do is practice your
serve (and try to get a net).
I expect that, as a group, that is what you *will* do.
Ralph Hartley
Serenus Zeitblom
> However, I don't see this tiny branch of science as being
> representative of science as a whole. When one reads a journal
> like Science or Nature one is forcefully reminded that these days,
> science is dominated by biology and its applications to medicine.
I strongly disagree with this. Science and Nature are basically
biology journals these days, so the prominence of biology in
their pages is not an occasion for surprise. And as for levels
of scientific integrity --- well, look at the amazing amount of
publicity given to the sequencing of the human genome: an
"achievement" of no more real fundamental scientific significance
than the sequencing of the porcupine genome. Then again, look at
the Proceedings of the National Academy of Sciences, a supposedly
prestigious journal full of total bullshit like mathematical
economics.....THE most important science of 2003 was the
announcement of the WMAP data, which will not be published
in Nature or Science. And how many papers does Ed Witten have
in the PNAS?
John Baez
Lubos Motl <mo...@feynman.harvard.edu> wrote:
>On Tue, 30 Sep 2003, John Baez wrote:
>> I believe that high-energy particle physics has entered a
>> somewhat decadent phase where less emphasis is being placed
>> on either matching the results of experiments *or* mathematical
>> rigor. It's becoming a bit like playing tennis with the nets down.
>Although I might also feel some reasons to call the very new era
>"decadent", I totally disagree with the description of the reasons and
>the symptoms.
Whew - for a second I was afraid you might agree with something I said!
My eyebrows were just shooting up to the top of my forehead when the
words "totally disagree" came along, and they came back down.
>Theoretical physics was never a part of mathematics, [...]
Once there were very good theoretical physicists who were
also very good mathematicians, like Newton, Leibniz, Laplace,
and Gauss. Some even taught in mathematics departments, like
Maxwell. However, I would never say that theoretical physics
was "part of mathematics", just that the overlap between the
two fields has at times been so high as to make it hard to
decide whether someone was a mathematician or physicist.
But this was no longer true in the 20th century, which is
probably your real point.
>and the culture of the physicists is different from the culture
>of the mathematicians.
Yes, that has certainly been true during the 20th century.
It was especially true in particle physics, when at least
before the discovery of the Z the flow of new experimental
data was so rapid that nobody had the slightest chance of
making theories rigorous at anywhere near the rate they
were being invented. It was much less true in general
relativity: for quite a while, this subject was dominated
by rigorous work due to people like Bergmann, Newman, Geroch,
Penrose, Hawking and others - and I'm leaving out lots of
important names here. One reason is that there weren't too
many experiments in general relativity until the 70s, and
most of them simply confirmed general relativity. Another is
that we've succeeded in formulating general relativity in a
rigorous way, unlike quantum field theory.
>Theoretical particle physicists try to investigate the topics at the very
>edge of our current understanding of the Universe. And this is a place
>where the optimal mathematical formalism has not been settled yet - and it
>usually takes a lot of time before the well-established theories are
>translated into a strictly rigorous mathematical framework. Consequently,
>it is usually counter-productive to insist on the mathematical rigor as
>the mathematicians know it.
That's certainly true when people are making rapid progress in
explaining the results of experiments. My point was that a
situation where theoretical physics is subject neither to
experimental test nor the test of mathematical rigor, it gets
harder to make sure one is on the right track. There's the danger
of fashions becoming established as dogma, and conjectures becoming
accepted as facts. And I'm afraid this is starting to happen.
>What is different about our era is that we are not aware of any
>experiments that truly and clearly enough contradict our previous theory
>of Nature - namely the pragmatic (but inconsistent) union of general
>relativity (with the cosmological constant included) and the standard
>model (with the neutrino masses included).
We've discussed this before, and you seem to be forgetting the fact
that besides the 4% of the energy density that's explained by the
Standard Model and the 73% that's "explained" by the cosmological
constant, there is a hefty 23% in the form of "cold dark matter",
which appears to be explained by neither the Standard Model +
massive neutrinos *nor* general relativity with cosmological
constant. Unless perhaps you're talking about ultra-massive
neutrinos serving as WIMPs... which is really quite a controversial
theory, and not part of what most people call the Standard Model.
I think it's quite remarkable that such a smart physicist as you
could say we're not aware of any experimnts that clearly contradict
our previous theory of Nature, when about 6 times as much matter
consists of some completely mysterious unknown stuff than the
amount that's explained by our theories! I think this is
symptomatic of how theoretical high-energy physicists have
become more interested in working out the logical consequences
of string theory than in explaining the data at hand.
>We know that this "theory" is good but not good enough, but we
>can only make progress without the new experimental data.
Luckily the astrophysicists are busy getting new data: for
example, the numbers I mentioned above are taken from WMAP,
the Wilkinskon Microwave Anisotropy Probe (WMAP). The
astrophysicists are also making good progress on testing
the inflationary cosmology, and thus indirectly testing ideas
on spontaneous symmetry breaking beyond the Standard Model.
They also found the best evidence for neutrino masses. And
eventually, LISA may detect the polarization of the gravitational
background radiation, which would open a window to the ultra-early
universe - back when gravitational waves hadn't decoupled from
the other forces.
So, there's new experimental data, and one huge unexplained
puzzle in particle physics waiting for some theorists to tackle
it: dark matter.
But, I'm not saying it's easy to make progress right now.
>> However, I don't see this tiny branch of science as being
>> representative of science as a whole. When one reads a journal
>> like Science or Nature one is forcefully reminded that these days,
>OK, let me still view these journals as representatives of popular and
>applied science, not pure science.
"Popular" and "applied" science? Have you tried reading many of
the actual papers in those journals, as opposed to the expository
articles in front? Here's how a physics paper taken from the latest
issue of Science starts off:
Dirac (1) postulated in 1931 the existence of a magnetic monopole (MM),
searching for the symmetry between the electric and magnetic fields in
the law of electromagnetism. A singularity in the vector potential is
needed for this Dirac MM to exist. Theoretically, the MM was found (2,3)
as the soliton solution to the equation of the non-Abelian gauge theory
for grand unification. However, its energy is estimated to be extremely
large, 10^{16} GeV, which makes its experimental observation difficult.
In contrast to this MM in real space, one can consider its dual space,
namely, the crystal momentum (k-) space of solids, and the Berry phase
connection (4) of Bloch wave functions. This MM in momentum space (5)
is closely related to the physical phenomenon of the anomalous Hall effect
(AHE) observed in ferromagnetic metals.
(taken from http://www.sciencemag.org/cgi/content/full/302/5642/92)
I wouldn't call that "popular" or "applied". One thing it does have,
which most modern papers in high-energy theoretical particle physics
don't, is experimental verification of the theories proposed.
I don't think Science accepts many theoretical papers that don't
contain some evidence that the theories are correct.
>More concretely, I don't think that a particle physicist should
>be proud if his or her paper is published in one of these journals.
I'm not sure most of their papers would be accepted.
Jeffery
ba...@galaxy.ucr.edu (John Baez) wrote in message news:<blcdtg$l27$1...@glue.ucr.edu>...
> In article <24a23f36.0309...@posting.google.com>,
> Thomas Larsson <thomas_l...@hotmail.com> wrote:
>
> >Page 51, middle:
> >
> >"some people have even begun to suggest that we relax our criteria
> >for establishing scientific fact. [...] According to a leading
> >science historian, such a subtle but ultimately sweeping
> >philosophical shift in theory justification may already be underway.
>
> Who is this mysterious unnamed "leading science historian"?
>
> >Without such a rigorous standard of truth, science will have little
> >defence against the onslaughts of the creationists and
> >postmodernists. "
Creationists and postmodernists pose zero threat to science. They are
at most a minor annoyance.
>
> I believe that high-energy particle physics has entered a
> somewhat decadent phase where less emphasis is being placed
> on either matching the results of experiments *or* mathematical
> rigor. It's becoming a bit like playing tennis with the nets down.
It's not the fault of theorectical particle physics that we don't yet
have the technology to reach the stupendous energies their theories
deal with. Since the early 1970's, theorists have been devoted to
explaining previously unexplained aspects of the Standard Model. Of
course there is much that is still unexplained, and there always will
be.
>
> However, I don't see this tiny branch of science as being
> representative of science as a whole.
It might be a "tiny branch" in terms of the percentage of physicists
or scientists that are working on it, but it represents over 99% of
the importance of physsics, science, or all human endevour. High
energy physics, particle physics, and cosmology is the attempt to
explain the entire Universe. I consider that the only real physics.
Everything else is insignificant in comparison. Particle physics is
the study of the Universe. Biology is the study of the life on this
one single insignificant planet orbiting an insignificant star that is
one of 100 billion stars in an insignificant galaxy which is one of
100 billion galaxies in the observable Universe. Now compare the
importance of biology to the importance of particle physics. There's
no basis of comparison. Particle physics and cosmology is the only
real physics, since it's attempting to explain the actual Universe
itself, and all other fields of physics, much less any other subject,
are of neglible significance in comparison.
When one reads a journal
> like Science or Nature one is forcefully reminded that these days,
> science is dominated by biology and its applications to medicine.
> Here empiricism is still perfectly alive and well, despite a certain
> amount of fraud due to the big bucks involved.
>
> So, I think that this "leading science historian" and the author of
> the article you quote are being overly alarmist.
>
> However, I think we must *constantly* fight to prevent the
> gradual rotting away of good scientific practice. To avoid
> "truth decay", we must *always* emphasize the difference
> between what we know, what we believe on the basis of pretty good
> evidence, what we suspect on the basis of a little evidence,
> what would be cool if it were true, what is fashionable this year,
> etc.
We'll never know the real truth about the real Universe anyway. It's
intrinsically unknowable. The purpose of physics is not to know the
real truth about the real Universe. We'll never know that. It's
unknowable. The purpose of physics is to think of theories that could
possibly explain what you observe.
Imagine drawing a horizontal line about a yard long on the chalk board
where the left end point represents the view of the universe possessed
by the first humans, and the right end point represents the truth of
the real Universe. Throughout history everyone has always assumed that
their view of the universe was about an inch from the right hand side.
Imagine putting a mark on the line about inch from the right hand
side. Everyone always thinks that unlike the past, they are finally
close to the truth. In Ancient Greece, the Renaissance, Newton, the
19th Century with Maxwell, the 1920's with relativity and quantum
mechanics, the 1940's with Feynman, the 1960's with quarks and the Big
Bang, the 1970's with Standard Model, the 1980's with grand
unification, supersymmetry, and superstrings, and inflation, and today
with M-theory, AdS/CFT, brane worlds, etc. they always thought they
were "close to" the real truth about the Universe, and they have
always been proven wrong. It's never been true in the past. It's not
true now. It's never be true in the future. Now imagine erasing the
right end point, and imagine the real right end point is three light
years to the right, on this scale. Do you actually think we'll ever
get anywhere close to the other side of this line? It was remarkable
arrogance for people in the past to think they were close to the
truth. Is it any less remarkable arrogance to think we'll ever be
close to the truth? The purpose of physics is not to find out the real
truth about the real Universe. That's unattainable. The purpose of
physics is to think up explanations that could possibly explain what
you observe.
Jeffery Winkler
Doug Goncz
>From: thomas_l...@hotmail.com (Thomas Larsson)
>Personally, I find it extremely disturbing that most physics
>professors, by their passivity, are allowing this paradigm shift to
>occur.
Are they? Most? It only take one, not even a professor, to inititate a paradigm
shift, right or wrong.
>http://www.aip.org/pt/vol-56/iss-8/p50.html
>
>Here are some key quotes:
>According to a leading
>science historian, such a subtle but ultimately sweeping
>philosophical shift in theory justification may already be underway.
>
May.
I translate that as "I, a science historian and creationist, have met at least
one person who agrees with me that the standards should be loosened enough to
make a B.A. in physics a _fine_ art degree."
Can you show that this has not happened?
Yours,
Doug Goncz (at aol dot com)
Replikon Research
Read the RIAA Clean Slate Program Affidavit and Description at
http://www.riaa.org/
I will be signing an amended Affidavit soon.
John Mitchell
>On Tue, 30 Sep 2003, John Baez wrote:
>
> ...
>> However, I don't see this tiny branch of science as being
>> representative of science as a whole. When one reads a journal
>> like Science or Nature one is forcefully reminded that these days,
>
>OK, let me still view these journals as representatives of popular and
>applied science, not pure science. More concretely, I don't think that a
>particle physicist should be proud if his or her paper is published in one
>of these journals.
>
>Best wishes
>Lubos
If physics is still grounded in empiricism, what accounts for your
condescension toward the empirical science published in those
journals? That privilege used to be reserved for mathematicians.
John Mitchell
Steve R Blattnig
> The best particle physicists can realistically expect to do now is
> to prepare for the day when new data starts coming again, try to
> hasten that day, and refrain from throwing stones.
There's lots of things that particle physicists are doing that's
directly connected to data. There's work on neutrino masses, searches
for possible phase transitions, lots of stuff in lattice QCD, even
more mundane things like pion production. There's monte carlo
simulation that work well, but that's far from being completely
explained.
Steve
John Baez
Serenus Zeitblom <serenusze...@yahoo.com> wrote:
>ba...@galaxy.ucr.edu (John Baez) wrote:
>> However, I don't see this tiny branch of science as being
>> representative of science as a whole. When one reads a journal
>> like Science or Nature one is forcefully reminded that these days,
>> science is dominated by biology and its applications to medicine.
>I strongly disagree with this. Science and Nature are basically
>biology journals these days, so the prominence of biology in
>their pages is not an occasion for surprise.
Science is the journal of the American Association for the
Advancement of Science. If you consider Science to be
"basically a biology journal these days" despite the fact
that it publishes research papers on almost every branch of
science, this is largely because there are more biologists
than, say, physicists or chemists or astronomers! They
publish more papers, get more grant money, and are dominant
in many other ways. This is what I meant by science being
dominated by biology. I wasn't saying biology is "better" -
that's too subjective a claim for me to bother with, and
not on-topic here on sci.physics.research. My point was
simply that declaring a trend away from empiricism in
the sciences based on the behavior of theoretical high-energy
particle physicists is a bit like declaring a major economic
trend in Europe based on statistics from one canton in
Switzerland: it's just too small and unrepresentative a sample!
We can also get some sense of what I mean by examining the
2001 budget of the National Science Foundation:
mathematics: $121 million
astronomy: $149 million
chemistry: $154 million
physics: $187 million
material science: $209 million
computer science: $487 million
biology: $485 million
This is sort of misleading because biologists also get
money from the National Institute of Health, and experimental
particle physics gets money from the Department of Energy,
and the Department of Defense contributes a lot of money
to various projects... but one gets the rough idea, especially
if one remembers that theoretical high-energy particle physics
is a fairly small province of physics.
Borcis
Lubos Motl wrote:
> On Tue, 30 Sep 2003, John Baez wrote:
>
>>I believe that high-energy particle physics has entered a
>>somewhat decadent phase where less emphasis is being placed
>>on either matching the results of experiments *or* mathematical
>>rigor. It's becoming a bit like playing tennis with the nets down.
>
> Although I might also feel some reasons to call the very new era
> "decadent", I totally disagree with the description
> ...this is a place
> where the optimal mathematical formalism has not been settled yet - and it
> usually takes a lot of time before the well-established theories are
> translated into a strictly rigorous mathematical framework. Consequently,
> it is usually counter-productive to insist on the mathematical rigor as
> the mathematicians know it.
> ...The physicists - unlike mathematicians - were always using "plausibility"
> arguments that were not 100% certain, and it will be so until the
> hypothetical discovery of the theory of everything.
Why and how should the TOE change that state of matter ? Also, do you really
believe anybody can learn or like physics without any appreciation for the
tradition of physics to mix mathematics like painters mix pigments ?
> The reason why we
> can't be quite 100% sure about something is that the object that we want
> to understand is the real world that was created by God/Nature, and not a
> system of mathematical axioms that are invented by the people.
To me it is rather unclear that
- "understanding a (set) system of axioms" is a faithful portrait of the
purposes and ways of professional mathematicians.
- 100% certainty is a uniform consequence of dealing with the systems of
axioms typically adopted by mathematicians. As a matter of fact, I thought
that the reason of the celebrity of Goedel's theorem was precisely that it
denied this (in the sense this had until then).
- more figuratively, that "the people" you cite, should share the Almighty's
logical incapacity to make a Stone that He can't move.
My perception here is that you confuse a rather traditional consumer view of
mathematics for a producer's view. Have you read Lakatos's "Proofs and
refutations" for a classic ?
> If you
> invent your own axioms without the trial-and-error method to refine your
> results and exclude the wrong conjectures, it is very likely that these
> axioms won't apply to the real world. I think that many people should
> re-read this favorite statement of Einstein's.
To what real tests did you put this assumption ? There are two extreme
antipodal strategies to deal with a statement that diverges from your own
well-informed opinion : one is to interpret it as the expression of the most
stupid state of mind (according to your measure) that's consistent with the
statement, the other is to interpret it as the most intelligent (under the
same constraints). Neither is particularly realistic, but if the purpose is to
use the energy of the debate to further the most interesting issues, rather
than classifying peoples' minds, the second is clearly the best of the two.
OTOH the first strategy is most efficient in the sense of allowing reuse of
the same components from one debate to the next - if you are not afraid of
solipsism.
> ...But those who stay must choose their methods
> that reflect the current abilities of physics to do experiments, and in
> this scheme of thing, mathematical consistency plays a more important role
> than it did in the past. I say "mathematical consistency" which is
> something different than "formal mathematical rigor"!
Your whole diatribe (together with jb's tennis metaphor) reminds me of a
phrase by one of the workers of the proof of the theorem of classification of
finite simple groups; I've been unable to find the exact citation; alluding to
the famous complexity of that proof, it was an expert's opinion going
something like "The probability that there is an error in the proof is close
to 1, but the probability that any such error can't be rectified is close to 0".
If there is a reasonable difference to make between the imperative of
mathematical rigor and that of mathematical consistency as applying to the
intuitions of particle physicists, the logic of that sentence imo illustrates
it (once transposed away from its original context).
By the same logic one should prefer the following hypothesis, and either
explore its consequences (for a more interesting debate) or require measurable
evidence to the contrary, *before* building castles over its rejection :
"Mathematical rigor according to Baez is, in the above context, equivalent to
mathematical consistency according to Motl"
Best wishes, Boris Borcic
--
12 ? - the least "integer" symbolizing all "integers" just by itself.
Successors : 123, 1234...
~
Serenus Zeitblom
Lubos Motl <mo...@feynman.harvard.edu> wrote in message
>
> OK, let me still view these journals as representatives of popular and
> applied science, not pure science. More concretely, I don't think that a
> particle physicist should be proud if his or her paper is published in one
> of these journals.
I agree, but I'd like to hear some debate as to where particle physicists
*should* be proud to publish. What are the good journals? Is Phys Rev D
the "best"?
Steve R Blattnig
On 2 Oct 2003, Peter Shor wrote:
> we're again in the situation that known theories can explain nearly
> all experimental observations.
I've heard statement like this many times and I've never understood them.
Do you really mean "known theories can explain all experimental
observation," or do you mean known theories aren't directly contridicted
by experimental observation. I can see some justification for the latter
statement but little for the former.
Steve
Joris Vankerschaver
jeffery...@mail.com (Jeffery) wrote in message news:<325dbaf1.03093...@posting.google.com>...
> > However, I don't see this tiny branch of science as being
> > representative of science as a whole.
>
> It might be a "tiny branch" in terms of the percentage of physicists
> or scientists that are working on it, but it represents over 99% of
> the importance of physsics, science, or all human endevour. High
> energy physics, particle physics, and cosmology is the attempt to
> explain the entire Universe. I consider that the only real physics.
> Everything else is insignificant in comparison. Particle physics is
> the study of the Universe. Biology is the study of the life on this
> one single insignificant planet orbiting an insignificant star that is
> one of 100 billion stars in an insignificant galaxy which is one of
> 100 billion galaxies in the observable Universe. Now compare the
> importance of biology to the importance of particle physics. There's
> no basis of comparison. Particle physics and cosmology is the only
> real physics, since it's attempting to explain the actual Universe
> itself, and all other fields of physics, much less any other subject,
> are of neglible significance in comparison.
That's a pretty, ahem, *arrogant* statement to make. There are
profound truths in every branch of human endavour and if you think HEP
is the only worthwhile undertaking in life or in physics, you might
need to take a few steps back and look at the big picture. Consider
for example the impact that Darwin's theory of evolution had on our
thinking. What Darwin said is true for this tiny grain of dust which
we inhabit, but will also hold for every possible form of life in the
universe. I wouldn't call that insignificant. Neither would I call a
detailed understanding of, for example, the working of the brain or
things like morfogenesis negligible.
You might not agree with him, but Roger Penrose has some tentative
arguments on the importance of biology for the understanding of our
universe. Even if he's wrong, there's still no a priori reason to
dismiss biology as something inherently nonfundamental.
> We'll never know the real truth about the real Universe anyway. It's
> intrinsically unknowable. The purpose of physics is not to know the
> real truth about the real Universe. We'll never know that. It's
> unknowable. The purpose of physics is to think of theories that could
> possibly explain what you observe.
OK. I observe *a lot* of physical phenomena that have little or
nothing to do with particle physics. I make up theories to explain
them. By your criterion, I'm doing physics although you consistently
refer to anything different from particle physics or cosmology as
"insignificant"...
Don't get me wrong, I like high energy physics as much as the next
guy, but I think it's unwise to be so focussed on one topic.
Cheers,
Joris Vankerschaver
Lubos Motl
> I agree, but I'd like to hear some debate as to where particle
> physicists *should* be proud to publish. What are the good journals?
> Is Phys Rev D the "best"?
That's of course a much more creative question. Among many theoretical
particle physicists there is a growing feeling that these printed journals
became "expensive dinosaurs" - especially those from Elsevier.NL like
Nuclear Physics B. I am certainly not an excited enemy of these journals -
and I rarely refuse to act as a referee for them - but some people would
like them to die, especially because poor universities can't afford to buy
NPB.
Physical Review D is, of course, much cheaper than Nuclear Physics, for
example. JHEP (jhep.sissa.it) is a refereed electronic journal that was
created to be essentially free, and many string theorists find JHEP to be
the only "politically correct" place to publish. At any rate, there is a
growing number of articles - even good articles - that only appear on the
arXiv. Physics is organized differently and physicists - at least the
particle ones - are more independent. At least today it is the case. They
would never be impressed by the label "New York Times", "Nature" or any
other "prestigious" place to publish. It is probably more interesting to
know how many citations a paper has than where it was published, and
these two things are almost independent.
Jeffery
news:<c7fd6c7a.0310...@posting.google.com>...
> Lubos Motl <mo...@feynman.harvard.edu> wrote in message:
> > John Baez wrote:
> > > [...] Science or Nature [...]
> > OK, let me still view these journals as representatives of popular
> > and applied science, not pure science. More concretely, I don't
> > think that a particle physicist should be proud if his or her
> > paper is published in one of these journals.
> I agree, but I'd like to hear some debate as to where particle
> physicists *should* be proud to publish. What are the good journals?
> Is Phys Rev D the "best"?
Yes, I would agree that Phys Rev D is the best. It's the journal I
subscribe to. It's expensive. It costs $200 a year.
Jeffery Winkler
Lubos Motl
> Science is the journal of the American Association for the
> Advancement of Science.
This is just some official description which does not change anything
about the validity of the claim that Nature is more or less irrelevant for
particle physics - and probably for all of physics - today.
> If you consider Science to be "basically a biology journal these days"
> despite the fact that it publishes research papers on almost every
> branch of science, this is largely because there are more biologists
> than, say, physicists or chemists or astronomers!
Well, I hope that there is a universal agreement that even if this
counting is correct, it does not make Nature a journal that is important
in any sense for physics professionals. There might be many people in
India, but it does not mean that India is the right place to study native
Americans (although Columbus was confused about this point). One can be
the strongest native American in India, but it does not make him the
strongest native American.
Otherwise, I hope that it is still true - and legal to write on
sci.physics.research - that physics is the most fundamental science in the
sense that others can follow from it, but not the other way around.
> We can also get some sense of what I mean by examining the
> 2001 budget of the National Science Foundation:
Not bad; the fraction of physics in Nature is certainly much smaller.
Best wishes
Lubos
Kris Kennaway
In article <9b2e17b4.03100...@posting.google.com>, Peter
Shor wrote:
> Yes, but the consensus that the ultimate theory of the universe has to
> a string theory seems to me dangerously premature. Could you try to
> explain to us laymen why the fact that string theory predicts that the
> world is ten-dimensional means that we shouldn't start looking for other
> ways of finding a theory of quantum gravity that accomodate a 4-dimensional
> world (which would indeed agree more with experiment :-) ...)?
One of the most important lessons from string theory over the past 6
years is that supersymmetric (and even certain non-supersymmetric)
quantum field theories in four dimensions are exactly dual to string
theories in 10 dimensions (when you decouple gravitational modes of
the string), in the sense that they contain the same information and
compute the same values for physical observables. Actually this
correspondence has yet to be tested for Kahler terms of N=1 theories,
but it is well established in all other aspects (e.g. N=1
superpotentials, and N>1 theories), and it is very suggestive that the
correspondence extends further, if only we could perform the
technically-difficult calculations.
This is a remarkable fact, and effectively means that if supersymmetry
is realised in nature above some energy scale, then -- _whether or not
string theory is the correct theory of quantum gravity at the planck
scale_ -- it is nonetheless a useful tool for understanding and
computing the structure of the supersymmetric phase of the field
theory, because it essentially translates four-dimensional quantum
field theory into 6-dimensional classical geometry (on the internal
compactified space).
Moreover, any other quantum theory of gravity that describes
supersymmetric field theories at low energy must also be equivalent in
this limit to strings propagating on a Calabi-Yau.
Kris
A.J. Tolland
>
> I strongly disagree with this. Science and Nature are basically
> biology journals these days, so the prominence of biology in
> their pages is not an occasion for surprise.
Did you consider the possibility that they are primarily biology
journals these days because there's more new and exciting science being
done in biology than anywhere else?
> And as for levels of scientific integrity --- well, look at the amazing
> amount of publicity given to the sequencing of the human genome: an
> "achievement" of no more real fundamental scientific significance than
> the sequencing of the porcupine genome.
Judging scientific work by the level of publicity it gets is a
waste of time and effort. Particularly when the publicity was largely a
function of (a) J.C. Ventner's competitive streak & commercial savvy, and
(b) man's fascination with himself.
> Then again, look at the Proceedings of the National Academy of Sciences,
> a supposedly prestigious journal full of total bullshit like
> mathematical economics..... THE most important science of 2003 was the
> announcement of the WMAP data, which will not be published in Nature or
> Science. And how many papers does Ed Witten have in the PNAS?
Go learn the Black-Scholes equation (actually, you more or less
already know it). Use it to predict the prices of the options of your
choice. You may be surprised.
I more or less agree with you that the WMAP data is the most
interesting data in particle physics these days. But I'm not sure it's
the most interesting scientific discovery of 2003.
The goal of science (as I see it at least) is to understand our
world in terms which allow us to make accurate predictions. Reductionism
is fabulously useful for this purpose, but it's far from perfect. In
particular, it's fantastically difficult to predict the behavior of
complicated systems even when we have a good knowledge of the
constituents. I'm not just speaking of technical difficulties in doing
large computations; we have very little quantitative understanding of how
new macroscopic degrees emerge from microscopic ones.
Par example: despite the introduction of density functional
theory, we still don't have an accurate quantitative picture of the
dynamics of water condensation.
Ed Witten may be the most influential string theorist (and God
knows he's left his marks on a few branches of modern mathematics), but
judging the value of all papers in a journal by the absence of his smacks
of provincialism.
--A.J.
A.J. Tolland
>
> Once there were very good theoretical physicists who were also very good
> mathematicians, like Newton, Leibniz, Laplace, and Gauss.
.... Hamilton, Jacobi, ...
> But this was no longer true in the 20th century, which is probably your
> real point.
As far as I can tell, physics and math haven't even been all that
separate in the 20th century. Increasing specialization made it harder to
work on physics and mathematics both, but it's hardly impossible. Just
look at the influence Noether, Wigner, & von Neumann had on physics, or at
the influence Dirac & Einstein had on mathematics.
As near as I can tell, the major split between physics and
mathematics is the difficulties mathematicians have had in making
mathematical sense of quantum field theory itself. And even in this case,
it's not as if there hasn't been a lot of inspiration and exchange on more
peripheral matters, like solitons and topological field theory.
I sometimes wonder if the theoretical physicist's disdain for
modern mathematics comes from the difficulties they themselves had of
making sense of mathematics. Why trust mathematics when the theory you're
working with is obviously not mathematically sound? Or perhaps it was
that the algebraic/axiomatic/constructive quantum field theorists
contributed relatively little of immediate use to physicists?
--A.J.
Thomas Larsson
John Baez wrote:
> > However, I don't see this tiny branch of science as being
> > representative of science as a whole. When one reads a journal
> > like Science or Nature one is forcefully reminded that these days,
>
> OK, let me still view these journals as representatives of popular and
> applied science, not pure science. More concretely, I don't think that a
> particle physicist should be proud if his or her paper is published in one
> of these journals.
One reason why a there is a lot of medicine in Nature or Science is that they
are top-ranked journals in that field; the medicine equivalent of PRL. Off the
top of my head, the only journals of comparable stature in molecular medicine
would be New England Journal of Medicine, Cell, and Natural Genetics.
But I agree that this is not the place for particle physics.
Ioan Oprea
> And as for levels
> of scientific integrity --- well, look at the amazing amount of
> publicity given to the sequencing of the human genome: an
> "achievement" of no more real fundamental scientific significance
> than the sequencing of the porcupine genome.
As a medical student, I have to strongly disagree with you on this
point. Sequencing the human genome was indeed a significant
achievement because it opens the way towards the thorough analysis of
the genes' functions. And the fact that we "only" have about 33,000
genes came as a real surprise. (we would have expected a larger number
of genes for such a complex organism; this proves, once more, that
what really matters is the collection of genes, not their number).
i.o.
Lubos Motl
I found your contribution to the discussion about the current theoretical
physics interesting.
> theoretical high-energy physics is facing a situation that physics
> hasn't faced for roughly a century...
Yes, it might be a good analogy. Of course, string theorists usually
consider the incompatibility of GR and the Standard Model to be a
counterpart of the ultraviolet catastrophe or the the Morley-Michelson
experiments - which were the "details" that finally led to the revolutions
in the early 20th century physics. Until some experimental results are
available, we must try to hope that the quantum gravity puzzle is more
similar to the case of relativity - which Einstein essentially understood
without the help of the experiments - than to the case of quantum
mechanics whose every single development depended on the experimental
results. Of course, today we know enough so that we could have constructed
quantum mechanics *without* the input from experiments 100 years ago. But
perhaps we are naive in other respects, and we won't be able to do the
things that our grand-grandsons in 80 years will find trivial.
There might be other hints of a future revolution. Some people believe
that the cosmological constant is a superimportant hint that will
revolutionize our understanding of physics. I personally don't think so,
but it is certainly a possibility a priori.
> I'm also worried about string theory becoming the accepted doctrine
> without any experimental evidence, which means that alternative
> theories (like loop quantum gravity or, even worse, something new that
> somebody comes up with and that nobody has thought about before) may
> get rejected without having undergone any real scrutiny.
I don't think that *all* physicists are that dishonest so that they would
reject a conjecture without having good reasons to do so. Everyone knows
that I think that LQG is getting much more attention than it should be
getting, but such issues exist within string theory, too. How many people
should study 2-dimensional string theory and the c=1 matrix models? How
many people should study various supersymmetric models and their
symmetries? How important is this subfield or that subfield? Every
physicist has a slightly different opinion about these questions.
> An experience that leads me to believe this is happening is that I've
> mentioned to two string theorists John Preskill's idea that the
> dynamics of the universe may lose information (and so be nonunitary)
> on the Planck scale, but that this information loss is covered up by a
> natural quantum error correcting code.
If you guys from quantum computing tried to study how string theory
describes quantum gravity (and not only anyons), you might be able to
contribute an essential idea. These words about quantum correcting codes
sound very intriguing, but we don't see a mathematical formalism that can
reconcile quantum gravity with quantum computing. :-)
Concerning the information loss - it is good that the quantum correcting
codes covered up the information loss because John Preskill is also known
for his bet against Hawking+Thorne in which Preskill said that the
information is NOT lost in the black hole evaporation. I am certainly on
Preskill's side. ;-)
> experiments. Now, there's no experiments available that aren't well
> explained by the standard theories.
That's right. But don't forget that the new theories still have to agree
with the old phenomena (and the standard "models"). This is an extremely
constraining condition, and string theory is the only conceptually new
framework that is capable to contain all the previous theories i.e. to
predict a world that qualitatively agrees with the observed Universe.
> > The physicists - unlike mathematicians - were always using
> > "plausibility" arguments that were not 100% certain, and it will be
> > so until the hypothetical discovery of the theory of everything.
>
> Won't it be so even after the hypothetical discovery of this theory?
Once a "theory of everything" is discovered, we would find a solid
fundament that would allow us to derive its various consequences with
mathematical certainty. Of course, many problems would stay equally
difficult as they're today, but we could actually prove theorems about
Nature. The theory of everything is equivalent to knowing the axioms of
the Universe, in a sense.
> Actually, that's not the way mathematics is done, either. Inventing
> axioms usually leads to obscure and unimportant theories. The trick is
> inventing the right axioms. But this belongs to a different
> discussion.
I agree.
> What is this statement of Einstein's, anyway?
He was not probably the first one (and certainly not the last one) to
emphasize the difference between natural sciences and mathematics, but he
did it often. For example, if you read his "Mein Weltbild", you find a
sentence saying roughly that "Everything that is rigorous does not apply
to the real world, and anything that applies to the real world is not
rigorous."
> The question is whether it's possible to make progress without the
> experimental data (but if the alternative is giving up and telling all...
That's right, it's an open question. But it seems to me that the only
alternative to the answer "let's hope and try" is to abandon theoretical
physics, at least for some time. Of course, some of us will do so, but it
is extremely probable that regardless of our personal opinions, some
people will continue to do theoretical physics. ;-)
> And I assume it's possible that there won't be any solid data
> for much longer, if the Higgs particle is discoverd on schedule and
> there's no evidence of any physics beyond the standard model.
Which is a scenario that I don't believe too much, but we will see.
> Yes, but the consensus that the ultimate theory of the universe has to
> a string theory seems to me dangerously premature.
You know, the world "string theory" sounds too specific. The theory as we
know it today is much richer and it is connected with most good ideas that
mathematicians in related fields have found. String theory is not a theory
of strings anymore; branes and other objects play an equally fundamental
role, much like noncommutative geometry, K-theory and other mathematical
fields. Trust me that if you call the ultimate theory "string theory", you
don't lose almost any generality. Although string theorists are convinced
that the 10D and 11D SUSY vacua will remain to be a part of the
unification story, we don't know many other answers to the general
question "what is string theory?", and therefore it is conceivable that
the frameworks as different as loop quantum gravity may become, after some
refinement, a part of string theory. This has happened with 11D
supergravity, for example. The people who studied it also constituted an
independent subcommunity of physics community, but they were proved to be
a part of the same structure.
> Could you try to explain to us laymen why the fact that string theory
> predicts that the world is ten-dimensional means that we shouldn't
> start looking for other ways of finding a theory of quantum gravity
> that accomodate a 4-dimensional world (which would indeed agree more
> with experiment :-) ...)?
Of course, my answer is guaranteed not to sound convincing without the
mathematical formalism. But at any rate, it is extremely difficult to
reconcile Einstein's equations with the rules of quantum mechanics, and
according to our experiences with particle physics (i.e. Fermi's theory of
weak interactions), the divergences in the loop Feynman diagram involving
General Relativity signal that new physical effects are taking over at the
short distances. The spectrum of possible theories that are well-defined
even in the UV (=ultraviolet, short distances) was already very small for
the weak interactions - the standard model is inevitable, in a sense - and
because general covariance is an even more subtle group, the requirement
of consistency is even more constraining for gravity, and there is
probably a lot of physics at short distances that General Relativity
neglects (because its divergences are worse than those of Fermi's theory).
Because it is so difficult, we should consider any example that works very
seriously - and string theory works.
Although there is no proof that other attempts must fail, it is almost
guaranteed for the theories that propose that there is no new physics and
no new particles at very high energies. The divergences in GR are real,
and any attempt to "interpret them away" is guaranteed to be a failure, I
think. If we talk about uniqueness of string theory, I would recommend
e.g. Joe Polchinski's semi-popular article
http://arxiv.org/abs/hep-th/9812104
When he is explaining that "all roads lead to string theory", he also
mentions various examples how one could try to find alternatives, but as
soon as these alternatives start to work, he realizes that they *are*
string theory again.
> > all puzzles in the past - with the possible exception of the discovery of
> > quantum physics.
>
> For which discovery, experiments were crucial.
That's right. But our ancestors also did not know as much as we know
today. ;-)
Louis M. Pecora
<har...@aic.nrl.navy.mil> wrote:
> > OK, let me still view these journals as representatives of popular and
> > applied science, not pure science. More concretely, I don't think that a
> > particle physicist should be proud if his or her paper is published in one
> > of these journals.
>
> Well, you don't have much chance of getting a paper accepted by a primary
> journal like *Cell*, do you? :-)
>
> This is the kind of thinking that gives physicists a bad name.
I've got to agree. I certainly don't think of Science and Nature as
applied journals. Maybe John Baez didn't mean it, but the statement
smacks of arrogance. Only the elite few are doing _pure_ science.
This is the position that many particle and later quantum field theory
physicists put themselves in throughout the 70's and later. They
defined pure science to be, basically, what they did, then they could
sit back and shoot down anyone else as just doing applied work since
that work could be derived, "in principal", from their own. It made
for a convenient, Kipling-like "just-so" story. The story sold well in
physics departments and to physics students. I'm not saying that's
what was done in the Baez quote above intentionally, but we all (myself
included for a long time) bought into it.
There are myriad phenomena that cannot be derived from quantum field
theory. Yes, we think that maybe that would be a good goal some day --
to show that it can be done, but that derivation remains undone for
most of the universe around us, especially for biological systems.
Almost all complex phenomena have to be handle without recourse to QFT.
That requires original, logical thinking. Physicists can bring those
techniques they do so well to, for example, biology and many do. I
think they (we) would all get much further if we get away from labeling
anything outside of QFT/General Relativity/String theory as applied.
--
Lou Pecora
- My views are my own.
Lubos Motl
> Once there were very good theoretical physicists who were
> also very good mathematicians, like Newton, Leibniz, Laplace, ...
Yes, I agree with everything you said about the history of maths and
physics, and what I meant was their divorce in the 20th century, as you
pointed out very well.
> ... fashions becoming established as dogma, and conjectures becoming
> accepted as facts. And I'm afraid this is starting to happen.
Mathematical rigor simply does not help you. You might disagree with the
mainstream of physics community about the question "what happens beyond
the Standard Model", for example, but not too many people are going to
believe you that you have found a magical rigorous mathematical key that
allows you to answer all these questions in a better way than string
theorists are able to do - unless you are actually able to show this key.
What I want to emphasize is that even in the current era, formal
mathematical rigor is a much cheaper value than physical depth and
consistency of the theories. One can rewrite a meaningless theory into a
precise language of axioms and theorems, but it won't make this theory
more meaningful.
> We've discussed this before, and you seem to be forgetting the fact
> that besides the 4% of the energy density that's explained by the
> Standard Model and the 73% that's "explained" by the cosmological...
I don't like this overly materialistic counting of our ignorance. The fact
that we don't know what 95% of the Universe is made of does not mean that
we don't know 95% of the secrets about the Universe. The dark energy is
just one number - most likely the cosmological constant - that must be
calculated from the equations at the end, and the dark matter might be
composed of one particle that we may identify one day - for example some
sort of LSP (neutralino or other supersymmetric partners). 100 years ago,
people knew thousands of data (spectral frequencies) that they could not
explain. You are now talking about two numbers.
It is probably not the best moment to answer the question about the nature
of the dark matter. We know that it must probably exist, but the mere
information that it exists is not enough to make progress in physics.
Would you recommend all biologists who study insect to switch to elephants
because elephants are bigger?
> become more interested in working out the logical consequences
> of string theory than in explaining the data at hand.
And what about you? Have you explained the value of the cosmological
constant and the identity of the dark matter? Most of us don't try to
attack this question directly because we have very good reasons to believe
that it just can't be attacked directly, and many other questions will
have to be answered first.
> Luckily the astrophysicists are busy getting new data: for
> example, the numbers I mentioned above are taken from WMAP,
> the Wilkinskon Microwave Anisotropy Probe (WMAP). ...
Yes, I am happy about all these things, and they allow to restrict various
models of inflation (or its alternatives). We still don't understand the
principles that decide which inflationary models are theoretically OK and
preferred, which is a worse thing.
> "Popular" and "applied" science? Have you tried reading many of ...
Sure, I have.
> Dirac (1) postulated in 1931 the existence of a magnetic monopole (MM), ...
Sure, this is a popular article, too. It looks exactly as another popular
article that I just wrote into a similar Czech journal, and it is also
similar to your articles in SPR. Just to be sure: would you oppose to the
claim that "This week in math. physics" is popularization of science? Why
do you then think that this trivial article in Nature is not popular? I
have no clue. It certainly does not look like a new technical article for
professionals that contains new results.
> >More concretely, I don't think that a particle physicist should
> >be proud if his or her paper is published in one of these journals.
>
> I'm not sure most of their papers would be accepted.
And I'm not sure whether they should worry about that. A similar
statement, in an even more extreme form, also holds for the New York
Times. Well, it is also a very prestigious paper. Does it mean that all
the physicists who are interviewed by the NYT about their theories are
good physicists?
John McCarthy
At the beginning of the last century (at least according to
some accounts I've read), a lot of physicists thought that
physics was mainly solved, with only a few theoretical
inconsistencies (such as the ultraviolet catastrophe).
These inconsistencies were actually hints that quantum
mechanics and relativity existed, which of course were both
major revolutions.
I wonder if this is some kind of legend.
Spectroscopy was a total mystery. The Rayleigh-Ritz combination
principle said that the reciprocals of the wave lengths tended to
be the differences of a much smaller number of numbers, but there
was no explanation of these numbers before quantum mechanics.
Radioactivity had been discovered and had no explanation.
--
John McCarthy, Computer Science Department, Stanford, CA 94305
http://www-formal.stanford.edu/jmc/progress/
He who refuses to do arithmetic is doomed to talk nonsense.
Thomas Larsson
> >From: thomas_l...@hotmail.com (Thomas Larsson)
>
> >Personally, I find it extremely disturbing that most physics
> >professors, by their passivity, are allowing this paradigm shift to
> >occur.
>
> Are they? Most? It only take one, not even a professor, to inititate a paradigm
> shift, right or wrong.
I did not say that most particle physicists are doing things detached from
experiments themselves. However, we all know that during the past 20
years, a significant amount of work has been devoted to a field without
experimental connection. Somebody has allowed this to happen.
In a parallel thread, I recently pointed out that of string theory's main
suggestions (not falsifyable predictions, because string theory does not
deal in such old-fashioned notions), e.g. extra dimensions, supersymmetry,
new gauge bosons, massless scalars associated with moduli, and a large and
negative cosmological constant, *none* has been confirmed experimentally.
The only reactions to this was that my observations were boring (Bergman)
and premature (Motl). Is it really the consensus of the physics community
that it is boring and premature to demand that some 20,000 man-years of
taxpayer-financed work should result in some testable prediction?
I also wonder how well known string theory's complete lack of experimental
support is. Does the informed public know? Do most physicists know? Do
grant and tenure committes know? And if they don't know, are they better
off being kept in blissful ignorance?
Perhaps it is because I love theoretical physics more than I love
theoretical physicists that I worry about the future of this field. It is
reassuring that at least Riordan seems to share my concern.
Peter Shor
> ba...@galaxy.ucr.edu (John Baez) wrote:
> > In article <24a23f36.0309...@posting.google.com>,
> > Thomas Larsson <thomas_l...@hotmail.com> wrote:
> >
> > >Page 51, middle:
> > >
> > >"some people have even begun to suggest that we relax our criteria
> > >for establishing scientific fact. [...] According to a leading
> > >science historian, such a subtle but ultimately sweeping
> > >philosophical shift in theory justification may already be underway.
> >
> >
> > I believe that high-energy particle physics has entered a
> > somewhat decadent phase where less emphasis is being placed
> > on either matching the results of experiments *or* mathematical
> > rigor. It's becoming a bit like playing tennis with the nets down.
>
> It's not the fault of theorectical particle physics that we don't yet
> have the technology to reach the stupendous energies their theories
> deal with. Since the early 1970's, theorists have been devoted to
> explaining previously unexplained aspects of the Standard Model. Of
> course there is much that is still unexplained, and there always will
> be.
>
> >
> > However, I don't see this tiny branch of science as being
> > representative of science as a whole.
>
> It might be a "tiny branch" in terms of the percentage of physicists
> or scientists that are working on it, but it represents over 99% of
> the importance of physsics, science, or all human endevour. High
> energy physics, particle physics, and cosmology is the attempt to
> explain the entire Universe. I consider that the only real physics.
> Everything else is insignificant in comparison.
This is an extremely exaggerated version of a view that many physicists
today indeed hold. However, at the turn of the century, mathematicians
held roughly the same opinion of the importance of the foundations of
mathematics, for roughly the same reasons. Consider the fact that around
six of Hilbert's 23 problems dealt with foundations, and the reception
given to Principia Mathematica. But even though the foundations of
mathematics still contain many unsolved questions, these foundations have
diverged much farther from most mathematician's concerns, and are no
longer viewed as central. Compare the reception given to Woodin's
attempt at a definite answer to the question of the continuum hypothesis
(Hilbert's first problem), the fact that the seven Clay problems contain
not one question from mathematical logic, and the parable of the spiders
(one description of which can be found at
http://groups.google.com/groups?selm=83977%40netnews.upenn.edu). If
string theory doesn't reconnect with experiment relatively soon, I
suspect it may be in danger of having the same thing happen to it.
Peter Shor
Andrew Resnick
>
<snip>
> It might be a "tiny branch" in terms of the percentage of physicists
> or scientists that are working on it, but it represents over 99% of
> the importance of physsics, science, or all human endevour. High
> energy physics, particle physics, and cosmology is the attempt to
> explain the entire Universe. I consider that the only real physics.
> Everything else is insignificant in comparison.
<snip>
This is a ridiculous attitude, and one that contributes to the antipathy
felt towards the sciences by laypersons. Please use high energy physics
to explain how a car works. You can't, and you shouldn't. The current
interesting work in science is not in the elucidation of single layers
of explanation, but in the connections between layers. Theory without
experiment is just as useless as observation without explanation.
--
Andrew Resnick, Ph. D.
National Center for Microgravity Research
NASA Glenn Research Center
Lubos Motl
On Mon, 6 Oct 2003, Borcis wrote:
> Why and how should the TOE change that state of matter?
Once we learn the TOE - hypothetically - we will have all the necessary
tools to formulate physical laws in a totally rigorous mathematical
framework. This is what I mean by a TOE.
> Also, do you really believe anybody can learn or like physics without
> any appreciation for the tradition of physics to mix mathematics like
> painters mix pigments ?
I am not sure what tradition you really mean, but as long as I understand
your question, the answer is "yes". Physics should not "mix" mathematics,
and certainly not in the same arbitrary way like painters mix pigments!
Physics should describe real physical phenomena, and in order to do so, it
must use the language of mathematics - the part of mathematics that is
necessary in a given context, not the other parts of mathematics.
> To me it is rather unclear that
>
> - "understanding a (set) system of axioms" is a faithful portrait of the
> purposes and ways of professional mathematicians.
It depends which mathematicians etc., but if one looks at the mathematical
threads on sci.physics.research, it is a very faithful portrait. Someone
invented the definitions (defining axioms) of groupoids, sheaves,
categories and other things, and other mathematicians play with these
notions - strictly within the pre-defined rules - without asking whether
the definition is useful, good or appropriate.
> - 100% certainty is a uniform consequence of dealing with the systems of
> axioms typically adopted by mathematicians. As a matter of fact, I thought
> that the reason of the celebrity of Goedel's theorem was precisely that it
> denied this (in the sense this had until then).
This is a very wide-spread misunderstanding of Goedel's theorems. One of
them says that it is possible to find a statement (by the way, a statement
that is useless for any practical purposes) that can be neither proved nor
disproved in a pre-defined system of axioms, as long as this system is
consistent and at least as powerful as the axioms about integers. However,
the proof of this incompleteness theorem also proves, using a stronger set
of tools, that this statement is valid. One can't prove it with the
pre-defined rules, but it is possible to prove it "informally" with some
extra rules.
The other theorem due to Goedel shows that it is impossible to prove that
these systems of axioms are consistent as long as one only uses these
axioms themselves. Paradoxically, this is an evidence that the set of
axioms *is* consistent, because if it were inconsistent, it would allow us
to prove anything - both true and false statements, including the (false)
statement about the consistency of these axioms.
> - more figuratively, that "the people" you cite, should share the Almighty's
> logical incapacity to make a Stone that He can't move.
Yes, that's a very figurative description. A consistent theory - it does
not matter whether in mathematics or physics - does not allow the
existence of such a true Almighty.
> My perception here is that you confuse a rather traditional consumer view of
> mathematics for a producer's view.
Could you please supplement this sentence with another sentence with some
more nontrivial contents?
> Have you read Lakatos's "Proofs and refutations" for a classic ?
Nope. Do you think it is better than Polya?
> To what real tests did you put this assumption?
All tests. It has passed all of them, and it has been proved beyond any
reasonable doubt. Without you I would not believe that there can exist a
human being who would disagree with the statement that "randomly chosen
systems of axioms are unlikely to describe the real world".
> There are two extreme antipodal strategies to deal with a statement
> that diverges from your own well-informed opinion : one is to
> interpret it as the expression of the most stupid state of mind
> (according to your measure) that's consistent with the statement, the
> other is to interpret it as the most intelligent (under the same
> constraints). Neither is particularly realistic, but if the purpose is
> to use the energy of the debate to further the most interesting
> issues, rather than classifying peoples' minds, the second is clearly
> the best of the two. OTOH the first strategy is most efficient in the
> sense of allowing reuse of the same components from one debate to the
> next - if you are not afraid of solipsism.
OK, is it fine with you to conclude that this paragraph does not contain
anything substantial and can be ignored?
> If there is a reasonable difference to make between the imperative of
> mathematical rigor and that of mathematical consistency as applying to
> the intuitions of particle physicists, the logic of that sentence imo
> illustrates it (once transposed away from its original context).
Yes, it is a very different thing. In simple terms, mathematical rigor is
a rather superficial property of the specific way how people treat a
problem, while mathematical consistency is an important objective property
of a set of ideas that is independent of all the human beings.
> "Mathematical rigor according to Baez is, in the above context,
> equivalent to mathematical consistency according to Motl"
No, it's certainly not. For example, string theory is a mathematically
consistent theory but it is not treated as a rigorous mathematical system
but rather as a proposal for a physical theory. On the other hand, a
physical theory of groupoids is a rigorous axiomatic system, but as a
physical theory it is inconsistent.
alejandro.rivero
> somewhat decadent phase where less emphasis is being placed
> on either matching the results of experiments *or* mathematical
> rigor. It's becoming a bit like playing tennis with the nets down.
>
Particle physics joins ranks with astrobiology, origin of
life or ancient world archeology, to name some, in a peculiar
characteristic: it is a popular demand, but it is not really the
mainstream of science.
One is astonished, for instance, learning that Troyan archeology was
stopped from 1936 to circa 1995. In this time, How many popular
articles have been written about Schliemann and the quest for
the location of Homer' places?
Worse, people really thinks there are huge amounts of research being
done in these fields. So any fluctuation there is perceived by journalists
and would-be-historians as a crisis in the whole building.
---------
Other question is, can a science such a particle physics to be
done with the usual people? Because in empirical sciences,
human resources is not critical. A decent student can be
trained to it, and even if it s not so decent, there is still
the Experiment, the guide of Nature, and also a little bit
of dollars and competition, of course.
Thus univ & research uses a human selection system where
entusiam is not required. It is just a job. A analytical high-brained
job, yep. But just so. Just follow Nature and she will provide guide.
The scene for a mathematical physicist is, that he has not
guide. Except math, and he is not trained in mathematical rigour.
He can be trained with problems-to-solve, but then he becomes
a problem solver: he bands with others of his cast to attack some
new problem they have found, and then they wander in the bald,
no serius goal in mind.
Perhaps it is an area where emphasis should be done in
selecting {\it vocational} people, then training them towards
high-brainers or, at least, to be patient analists. It is
not easy, because the system runs against vocation. It
can be build when youngster, reading these divulgation
magazines I told before. But then one comes to the university
to discover that -with only one or two exceptions- no teachers has
even been working close to solve these issues, as they are not
really so interested.
Even if the discovery does not destroy its vocation, the
candidate will probably drift away to play with other interests:
computers, liquors, family... so he will not care enough of
his training. Of course, teachers do not care... as I told, they
only need to harvest the trained people at the end of the
formation period, do not worry about how vocational or
interested in Science he is.
Sorry the pesimism. Just in case some fresh 1st years is still
reading the group: please do not surrender, and keep doing all these
awful math exersises :-)
Alejandro
John McCarthy
Science is more than a biology journal.
It has a special interest in unmanned space exploration, and each
major spacecraft has had a collection of articles about its results.
It also publishes special issues on topics like energy (sometimes more
politically correct than correct).
Arnold Neumaier
Lubos Motl wrote:
>
> What I want to emphasize is that even in the current era, formal
> mathematical rigor is a much cheaper value than physical depth and
> consistency of the theories. One can rewrite a meaningless theory into a
> precise language of axioms and theorems, but it won't make this theory
> more meaningful.
This is not what is meant with rigor. Rigor means deriving results
without logical gaps, and this means for physics no ill-defined
limits or asymptotic series without a well-defined recipe for making
them produce exact numbers. From this point of view, practical quantum field
theory is presently outside formal mathematical rigor.
And it is much harder to make QFT rigorous than to pursue string
theory at the traditional level of sloppiness. So what is cheaper???
Arnold Neumaier
A.J. Tolland
On Wed, 8 Oct 2003, A.J. Tolland wrote:
> I sometimes wonder if the theoretical physicist's disdain for
> modern mathematics comes from the difficulties they themselves had of
> making sense of mathematics.
Eek. I have a horrible tendency to send off uncorrected posts.
Replace "of mathematics" with "of the mathematics of QFT".
No offense intended.
If you are offended, I suggest learning more math. :)
--A.J.
Tim S
> Peter Shor includes:
>
> At the beginning of the last century (at least according to
> some accounts I've read), a lot of physicists thought that
> physics was mainly solved, with only a few theoretical
> inconsistencies (such as the ultraviolet catastrophe).
> These inconsistencies were actually hints that quantum
> mechanics and relativity existed, which of course were both
> major revolutions.
>
> I wonder if this is some kind of legend.
I think it is. A few physicists may have thought this but I don't
think that most did. There were lots of open questions.
> Spectroscopy was a total mystery. The Rayleigh-Ritz combination
> principle said that the reciprocals of the wave lengths tended to
> be the differences of a much smaller number of numbers, but there
> was no explanation of these numbers before quantum mechanics.
>
> Radioactivity had been discovered and had no explanation.
Electromagnetism and thermodynamics were important, ongoing
programmes. The people like FitzGerald and Heavyside who had spent
decades trying to clarify Maxwell's theory had tried to do away with
charged particles altogether, and only keep the electric and magnetic
fields; and had just discovered that this didn't work. People were
even more confused about entropy than they are now. The heat
capacities of solids were a mystery. In fact, a lot of the early work
on relativity and quantum theory can be seen as a continuation of
existing research programmes in electromagnetism and thermodynamics.
Another major area of mystery was the microscopic structure of matter,
about which people knew almost nothing. There were lots of physics
questions on the border with chemistry: Did atoms exist and, if so,
what the hell were they? What was the physical nature of the forces
that bound atoms together in molecules and inorganic compounds? What
happened to substances when they dissolved? Were the particles that
existed in solution the same as the ones that existed in the solid
state? And if not, how were they related? Why were almost all (but not
absolutely all) atomic weights nearly (but not exactly) integer
multiples of that of hydrogen? What was the physical reason for the
periodic table?
Fluid dynamics was still a major area of research. Also, although I
don't know of actual work on the question, there was potentially the
issue of what determined the mechanical properties of materials
(surface tensions, elastic moduli, etc).
Plus questions that we now realise were fruitless, but were thought
important at the time -- e.g., What was the nature of the aether?
Tim
John Baez
Tim S <T...@timsilverman.demon.co.uk> wrote:
>on 8/10/03 7:25 am, John McCarthy at j...@Steam.Stanford.EDU wrote:
>> Peter Shor wrote:
>>> At the beginning of the last century (at least according to
>>> some accounts I've read), a lot of physicists thought that
>>> physics was mainly solved, with only a few theoretical
>>> inconsistencies (such as the ultraviolet catastrophe).
>>> These inconsistencies were actually hints that quantum
>>> mechanics and relativity existed, which of course were both
>>> major revolutions.
>> I wonder if this is some kind of legend.
>I think it is.
In 1894, Albert Michelson gave an address at the dedication ceremony
for the Ryerson Physical Laboratory at the University of Chicago.
In it, he said:
"The more important fundamental laws and facts of physical science
have all been discovered, and these are now so firmly established that
the possibility of their ever being supplanted in consequence of new
discoveries is exceedingly remote.... Our future discoveries must be
looked for in the sixth place of decimals."
Ironically, this is the Michelson whose experiment with Morley
became so important in convincing people that special relativity
is correct!
But, it's also worth noting that Michelson never quite came around
to believing in special relativity. After relativity was quite well
accepted by most good physicists, he wrote a famous article in the
Encylopedia Britannica in which he cast doubt on it. He was also
important in preventing Einstein from getting a Nobel prize for this
work. So, he was not what I'd call the most progressive of thinkers.
On the other hand, he couldn't have been an isolated case, because
even earlier, in 1871, James Clerk Maxwell felt obliged to refute
the idea that physics was almost done. He wrote:
"This characteristic of modern experiments - that they consist
principally of measurements - is so prominent, that the opinion
seems to have got abroad that in a few years all the great
physical constants will have been approximately estimated, and
the only occupation which will then be left to men of science
will be to carry on these measurements to another place of decimals."
He believed that this was completely wrong, and wrote:
"We are probably ignorant even of the name of the science which will
be developed out of the materials we are now collecting...."
Some other data points: Robert Millikan has written that physics
was widely regarded as a "dead subject" in the early 1890s. Max
Planck wrote that when deciding what to study at the University
of Munich in 1875, the professor of physics at this university told
him that nothing worthwhile remained to be discovered. And in 1888,
the American astronomer Simon Newcomb wrote:
"So far as astronomy is concerned, we must confess that we do
appear to be fast approach the limits of our knowledge."
So, there seems to be some truth to the idea that some people
underestimated how much there was left to learn back in the late 1800s.
.......................................................................
References:
Michelson quote:
http://www.madsci.org/posts/archives/dec98/912518006.Sh.r.html
other quotes, except for second quote by Maxwell:
http://www.cccu.org/doclib/20020528_Sep00.pdf
John Baez
Louis M. Pecora <pec...@anvil.nrl.navy.mil> wrote:
>In article <bleobt$oi2$1...@ra.nrl.navy.mil>, Ralph Hartley
><har...@aic.nrl.navy.mil> wrote:
>> [though not cited by Pecora, it was Lubos Motl who wrote]:
>> > OK, let me still view these journals as representatives of popular and
>> > applied science, not pure science. More concretely, I don't think that a
>> > particle physicist should be proud if his or her paper is published in one
>> > of these journals.
>> Well, you don't have much chance of getting a paper accepted by a primary
>> journal like *Cell*, do you? :-)
>>
>> This is the kind of thinking that gives physicists a bad name.
>I've got to agree. I certainly don't think of Science and Nature as
>applied journals. Maybe John Baez didn't mean it, but the statement
>smacks of arrogance.
I'm not sure which statement you're talking about, but I wrote
none of the text you quoted above. In a previous article, I had written:
I believe that high-energy particle physics has entered a
somewhat decadent phase where less emphasis is being placed
on either matching the results of experiments *or* mathematical
rigor. It's becoming a bit like playing tennis with the nets down.
However, I don't see this tiny branch of science as being
representative of science as a whole. When one reads a journal
like Science or Nature one is forcefully reminded that these days,
science is dominated by biology and its applications to medicine.
Here empiricism is still perfectly alive and well,
To this, Lubos Motl replied that he viewed these journals as
representatives of "popular and applied science". I later argued
against this view.
>This is the position that many particle and later quantum field theory
>physicists put themselves in throughout the 70's and later. They
>defined pure science to be, basically, what they did, then they could
>sit back and shoot down anyone else as just doing applied work since
>that work could be derived, "in principal", from their own. It made
>for a convenient, Kipling-like "just-so" story. The story sold well in
>physics departments and to physics students. I'm not saying that's
>what was done in the Baez quote above intentionally, but we all (myself
>included for a long time) bought into it.
Again, there was no "Baez quote above" in your post.
John Baez
Lubos Motl <mo...@feynman.harvard.edu> wrote:
>On Fri, 3 Oct 2003, John Baez wrote:
>> ... fashions becoming established as dogma, and conjectures becoming
>> accepted as facts. And I'm afraid this is starting to happen.
>Mathematical rigor simply does not help you.
I agree that it only helps a little. What theoretical high-energy
particle physicists really would like is feedback from experiment!
This is what used to keep them disciplined. But in the current situation,
they're not getting this discipline.
In part this is due to a shortage of new experiments and unexplained
data. In part it's due to lack of focus on the unexplained data that
actually exist. But it's partially due to their increasing interest
in working on models that are intrinsically beautiful but bear only a
rough resemblance to our universe - like string theory on 5-dimensional
anti-deSitter spacetime times a large 5-sphere.
To keep work on models like this from becoming ever more fanciful and
extravagant, mathematical rigor can be a useful form of discipline -
at least as a goal, even if it's hard to achieve.
However, I don't actually expect most theoretical particle physicists to
embrace this goal - unless the subject gradually gets pushed into the
math departments after decades of inability to make predictions concerning
experiments.
>You might disagree with the
>mainstream of physics community about the question "what happens beyond
>the Standard Model", for example, but not too many people are going to
>believe you that you have found a magical rigorous mathematical key that
>allows you to answer all these questions in a better way than string
>theorists are able to do - unless you are actually able to show this key.
I never claimed to have found such a magical key, so there's really
no issue of people "believing me" about this.
>What I want to emphasize is that even in the current era, formal
>mathematical rigor is a much cheaper value than physical depth and
>consistency of the theories.
Actually, mathematical rigor is nothing other than being sure one's
work is consistent - or at least as consistent as set theory. But,
I agree completely that a physical theory needs to be much more than
an arbitrary consistent set of axioms. It needs to describe our
actual universe - with all 11 dimensions, superpartners, D-branes,
and all. :-)
>> We've discussed this before, and you seem to be forgetting the fact
>> that besides the 4% of the energy density that's explained by the
>> Standard Model and the 73% that's "explained" by the cosmological...
>I don't like this overly materialistic counting of our ignorance. The fact
>that we don't know what 95% of the Universe is made of does not mean that
>we don't know 95% of the secrets about the Universe.
I never said it did. I was just correcting your claim that:
>>>What is different about our era is that we are not aware of any
>>>experiments that truly and clearly enough contradict our previous theory
>>>of Nature - namely the pragmatic (but inconsistent) union of general
>>>relativity (with the cosmological constant included) and the standard
>>>model (with the neutrino masses included).
The dozens of observations regarding dark matter are counterexamples
to this claim. And I should add that this is even true if dark matter
turns out not to exist! Because if dark matter does not exist, then
something *else* must be wrong with our theories.
>It is probably not the best moment to answer the question about the nature
>of the dark matter.
Maybe not - but it is one of the major unexplained phenomena in physics,
so it deserves a little effort.
>Would you recommend all biologists who study insects to switch to elephants
>because elephants are bigger?
Yes, unless they're allergic to elephants. Next question?
>>I think this is symptomatic of how theoretical high-energy physicists have
>>become more interested in working out the logical consequences
>>of string theory than in explaining the data at hand.
>And what about you?
I'm not a theoretical high-energy physicist. I teach in a mathematics
department and my job is to prove theorems. I work on n-categories
and loop quantum gravity. My excuse for working on a branch of physics
that has little input from experiment is that I'm proving theorems that
will remain interesting regardless of what happens. This does not
prevent me from handing out free advice to theoretical high-energy
particle physicists - advice they are free to ignore.
>Have you explained the value of the cosmological constant and the
>identity of the dark matter?
Yes. But I'm keeping it secret just to see how long it takes
the rest of you guys to figure it out.
>> Luckily the astrophysicists are busy getting new data: for
>> example, the numbers I mentioned above are taken from WMAP,
>> the Wilkinskon Microwave Anisotropy Probe (WMAP). ...
>Yes, I am happy about all these things, and they allow to restrict various
>models of inflation (or its alternatives).
Yay! We agree about something! Let's break out the champagne...
>We still don't understand the principles that decide which
>inflationary models are theoretically OK and preferred, which
>is a worse thing.
Yeah, that's a bummer.
>> "Popular" and "applied" science? Have you tried reading many of ...
>Sure, I have.
>> Dirac (1) postulated in 1931 the existence of a magnetic monopole (MM), ...
>Sure, this is a popular article, too. It looks exactly as another popular
>article that I just wrote into a similar Czech journal, and it is also
>similar to your articles in SPR.
Really? It reports on an experiment done with crystalline strontium
rubidium trioxide, comparing it with some calculations they did,
attempting to demonstrate the existence of a novel phenomenon related
to the anomalous Hall effect. A typical sentence looks like this:
Calculated (Calc., left panels) and experimental (Exp., right panels)
longitudinal (xx) and transverse (xy) optical conductivity of SrRuO_3
film. Measurements were performed at low temperature (10 K). Calculations
for both the orthorhombic single-crystal structure and the hypothetical
cubic structure kept the average Ru-O bond length.
I don't write stuff like this on sci.physics.research, that's for sure.
>Just to be sure: would you oppose to the claim that "This week in
>math. physics" is popularization of science?
You know I'd oppose anything just for the fun of arguing with you.
Seriously: most of TWF is popularization, but some of it is new
mathematics that James Dolan or I have invented - stuff that happens
to be more fun to explain to a large audience than to write up as
a traditional journal article.
>Why do you then think that this trivial article in Nature is not popular?
>I have no clue.
Well, if you consider stuff like this "popular", all I can do is
urge you not to try to write a best-seller:
As shown in Fig. 2 for the dependence of optical conductivity, the
high-energy (>0.5 eV) part, which is dominated by the p-d charge
transfer peak, is usual and can be well reproduced by our calculations,
whereas the observed peak structure of sigma_xy(omega) below 0.5 eV
is a clear demonstration of the predicted spiky behavior.
(This is another random passage from the article.)
John Baez
Jeffery <jeffery...@mail.com> wrote:
>ba...@galaxy.ucr.edu (John Baez) wrote in message
>news:<blcdtg$l27$1...@glue.ucr.edu>...
>> I believe that high-energy particle physics has entered a
>> somewhat decadent phase where less emphasis is being placed
>> on either matching the results of experiments *or* mathematical
>> rigor. It's becoming a bit like playing tennis with the nets down.
>> However, I don't see this tiny branch of science as being
>> representative of science as a whole.
>It might be a "tiny branch" in terms of the percentage of physicists
>or scientists that are working on it, but it represents over 99% of
>the importance of physsics, science, or all human endevour.
I don't feel that high-energy particle physics "represents
over 99% of the importance of all human endeavour". To me
this seems like a drastically skewed assessment of what life
is all about! But, I wasn't attempting to broach such a broad
subject as the overall meaning of our existence. I don't think
s.p.r. is the right place to discuss whether particle physics
is more than 99 times as important as having good sex, for
example. I was merely trying to remind people that we can't
extrapolate any claimed "trend away from objectivity" from
high-energy particle physics to science as a whole.
John Baez
A.J. Tolland <a...@math.berkeley.edu> wrote:
>On Fri, 3 Oct 2003, John Baez wrote:
>> Once there were very good theoretical physicists who were also very good
>> mathematicians, like Newton, Leibniz, Laplace, and Gauss.
>
> .... Hamilton, Jacobi, ...
>
>> But this was no longer true in the 20th century [....]
>As far as I can tell, physics and math haven't even been all that
>separate in the 20th century.
I certainly like to think of them as two poles of
a continuum rather than separate subjects; I think they
do much better together than apart. I would certainly
be miserable studying one without the other! However,
it's hard to argue with this: starting sometime in the
mid-1800s it became a lot easier to classify people as
either mathematicians or physicists. The disciplines
started acquiring more and more of their own disinct
habits of thought.
I wish I knew more about when and why this happened.
For all I know, maybe it happened sometime around when
mathematicians adopted the epsilon-delta definition of
"limit". Physicists have never been particular fond of
this: they still prefer to work with an intuitive version
of infinitesimals.
>Increasing specialization made it harder to work on physics and
>mathematics both, but it's hardly impossible. Just look at the
>influence Noether, Wigner, & von Neumann had on physics, or at
>the influence Dirac & Einstein had on mathematics.
Dirac and Einstein had an enormous impact on mathematics,
but nobody would ever mistake them for mathematicians.
Noether's theorem is one of the mainstays of modern physics,
but nobody would mistake her for a physicist. Von Neumann
and Wigner are among the few greats of the 20th century
who defy being classified as either mathematicians or
physicists. Poincare came close, but somehow winds up
falling on the mathematics side of the divide, I think.
(Von Neumann could also be considered one of the top computer
scientists of the 20th century. He was utterly amazing.)
>As near as I can tell, the major split between physics and
>mathematics is the difficulties mathematicians have had in making
>mathematical sense of quantum field theory itself.
That's true. Physicists worried about whether quantum
field theory a whole lot until the gauge theories of the
strong and weak interactions started succeeding - witness
Dirac and Feynman's agonies over the subject, and the days
when the "analytic S-matrix" and "current algebra" were
touted as ways to get some of the good results of quantum
field theory without having to accept the theory as a whole.
But once quantum field theorists got used to working in the
absence of rigorous foundations, they pretty much lost interest
in finding such foundations... and since most mathematicians
didn't want to work on a subject without clear foundations,
a wedge was driven between the two subjects.
Luckily, the work of Witten and other physicists have shown
mathematicians that quantum field theory is too powerful a
tool to neglect. (Witten is another person who resists
classification!) Now most good mathematicians *want* to
understand quantum field theory. I see this even in conferences
on homotopy theory and categories. But most quantum field theory
remains outside the scope of what mathematics can handle in
a rigorous way....
John Baez
>In article <Pine.SOL.4.44.0310022309240.3383-100000@blue1>,
>A.J. Tolland <a...@math.berkeley.edu> wrote:
>>As near as I can tell, the major split between physics and
>>mathematics is the difficulties mathematicians have had in making
>>mathematical sense of quantum field theory itself.
>Luckily, the work of Witten and other physicists have shown
>mathematicians that quantum field theory is too powerful a
>tool to neglect.
And luckily, Witten is using his influence to advocate work
on making quantum field theory rigorous! It's worth reading
what he says about this in the January 2003 issue of the
Bulletin of the American Mathematical Society:
Edward Witten, Physical law and the quest for mathematical understanding
http://www.ams.org/journal-getitem?pii=S0273-0979-02-00969-2
Abstract: The theoretical physics of the first quarter of the
twentieth century - centering around relativity theory and
nonrelativistic quantum mechanics - has had a broad influence
mathematically. The main achievement of theoretical physics
in the following half-century was the development of quantum field
theory or QFT. Yet the mathematical influence of QFT still belongs
largely to the 21st century, because its mathematical foundations
are still not well-understood.
Let me quote a bit:
Being a much more difficult theory than Relativity or Quantum
Mechanics, Quantum Field Thery has taken much longer to develop,
and it is much harder to establish the mathematical foundations.
Moreover the important constructions are subtle to describe and
at first sight may tend to look rather specialized to many
mathematicians. Rigorous models of QFT are hard to come by,
and when available (as in Sinai's lecture at this conference, and
in extensive developments in constructive field theory) they are
far from what is needed to get in touch with elementary particle
physics. Since the asymptotic freedom of quantum non-abelian
gauge theory was discovered in 1973, we have known what conjectures
one should aim to prove to give a proper mathematical foundation
to the standard model of particle physics. I will say more about
this later. But proofs have yet to appear.
The gap that therefore still exists is, I think, the main reason
that post-1925 theoretical physics is not better known mathematically.
I can think of at least three reasons that mathematicians may wish
to remedy this:
A) Understanding natural science ahs been, historically, an
important source of mathematical inspiration. So it is frustrating
that, at the outset of the new century, the main framework used
by physicists for describing the laws of nature is not accessible
mathematically. The same point has been made for decades, since
the start of axiomatic and constructive quantum field theory.
B) Although QFT is not yet widely recognized as a mathematical
subject, in the last 20 years or so, the QFTs that are important
in physics have proved to have many geometrical applications
that may be of interest even if one is not principally motivated
by physics. Examples include applications to:
* Donaldson theory of four-manifolds
* Jones polynomial of knots and related three-manifold invariants
* mirror symmetry
* cohomology of moduli spaces
* elliptic cohomology
* SL(2,Z) symmetry of characters of Kac-Moody algebras
C) Finally, life - and theoretical physics as such - did not end
when the standard model as such was completed by the mid-1970s.
[...] For many reasons, a knowledge of QFT is the basic prerequisite
for learning about string theory.
John C. Polasek
>
>Lubos Motl <mo...@feynman.harvard.edu> wrote in message
>> > like Science or Nature one is forcefully reminded that these days,
>>
>> OK, let me still view these journals as representatives of popular and
>> applied science, not pure science. More concretely, I don't think that a
>> particle physicist should be proud if his or her paper is published in one
>> of these journals.
>
>I agree, but I'd like to hear some debate as to where particle physicists
>*should* be proud to publish. What are the good journals? Is Phys Rev D
>the "best"?
>
Yes Serenus, but only if your title sounds a lot like the following
examples:
¨ Bianchi-type IX brane-world cosmology.
¨ Spontaneous baryogenisis in warm inflation
¨ Chaos and damping in the post-Newtonian description of spinning
binaries
¨ Killing reduction of 5-dimensional spacetimes
¨ Brane-world dynamics in conformal bulk field
¨ Affleck-Dine mechanism with a negative thermal logarithmic potential
¨ Observational constraints on cosmic string production during brane
inflation
¨ Noncommutative gravity: Fuzzy sphere and others
but not like:
¨ Vacuum: a proposed blueprint*
and be sure to have 4 other authors and a good school and funding by
NSF, NASA, etc.
Louis M. Pecora
In article
<Pine.LNX.4.31.031006...@feynman.harvard.edu>, Lubos
Motl <mo...@feynman.harvard.edu> wrote:
> Well, I hope that there is a universal agreement that even if this
> counting is correct, it does not make Nature a journal that is important
> in any sense for physics professionals. There might be many people in
> India, but it does not mean that India is the right place to study native
> Americans (although Columbus was confused about this point). One can be
> the strongest native American in India, but it does not make him the
> strongest native American.
>
Actually, Nature has a pretty good reputation in various areas of
physics like condensed matter and nonlinear dynamics. People in those
and some other sub-areas of physics are very happy to get a Nature
Paper.
alejandro.rivero
news:<24a23f36.0309...@posting.google.com>...
> In the August 2003 issue of Physics Today, there is an opinion piece
> by Michael Riordan, of Stanford and Santa Cruz, entitled "Science
> Fashions and Scientific Facts". This article can be found online at
>
> http://www.aip.org/pt/vol-56/iss-8/p50.html
> Page 51, middle:
> "some people have even begun to suggest that we relax our criteria
> for establishing scientific fact. [...] According to a leading
> science historian, such a subtle but ultimately sweeping
> philosophical shift in theory justification may already be underway.
I have been working recently (this is in the last five years) on two
instances where the interaction between mathematics and physics did
actually drive to a wrong turn.
One is at the third or fourth century BCE. At these time there was
some rudiments of calculus (Archimedes etc) and some sound conjectures
about physical reality (atomism, for one, had even deduced the need of
"penetrable" exchange particles to communicate between the
"impenetrable" fundamental ones). But the most impressive show of
mathematical reasonment was the clasification theorem for regular
solids. It was provedd that there are five and only five (in three
dimensions. Note there are infinite in 2 dim and only one (?) for d>3).
[Moderator's note: there are six regular polytopes in
dimension 4 and three in all higher dimensions; see
http://math.ucr.edu/home/baez/platonic.html for details. - jb]
As a consequence of this rigourous fact, the natural philosophers
extended four elements with a new one, quintessence, so that they map
naturally in the classification theorem. And this completely illogical
step, muddly backed in mathematics, was the standard theory of matter
for centuries.
The second instance is Newton Principia, Proposition 1. There has been
a lot of noise on it lately:
B. Pourciau, Arch. Hist. Exact Sci. 57 (2003), p 267
M. Nauenberg, Historia Mathematica (2003, In press)
H. Erlichson, Historia Mathematica (2003, In press)
see URLs:
http://www.sciencedirect.com/science/journal/03150860
http://www.springerlink.com/link.asp?id=my3kkf1afm0m
Beyond the general objection on the validity of differential calculus,
which was not mathematically sound at these times, there is the
question about how a set of zigzagging trajectories, very much a la
Feynman, can approach, in the limit, to a continous trajectory. It is
a tricky issue, involving impulses with instantaneus infinite
acceleration, to be smoothed over the time evolution, which in turn is
not an static geometrical entity, but one depending on a external
parameter, time.
Here it seems that it was accepted, as an input from Nature, the fact
of the existence of such trajectory. In this wrong turn, classical
mechanics was discovered.
The blame in both cases does not fall upon mathematics, but upon the
awe imposed by the mathematical framework, that eventually drove the
researchers to see a non-mathematical or non-rigourous step as if it
were a sound one. The wrong turn happens not in a far fetched theory
from a crackpot group, but in the most careful scientific framework of
the age.
On other hand, the results were different: in the first case an absurd
theory of Nature was raised as standard, and experimentalists were
driven to develop underground theories of their own (Sulfur+Mercury as
primary elements, for instance). In the second case a very
intelligent approximation to Nature was done, which has worked for
some centuries and it is still useful, even if eventually the whole
set of zigzagging paths, with adequate weighting, has resulted to be a
more correct explanation of reality.
Alejandro Rivero
Jeffery
news:<20031006093...@newsread.grc.nasa.gov>...
> In <325dbaf1.03093...@posting.google.com> Jeffery wrote:
> <snip>
> <snip>
Are you claiming that explaining how a car works is of equivalent
importance to explaining the Universe?
Jeffery Winkler
Arnold Neumaier
>
> starting sometime in the
> mid-1800s it became a lot easier to classify people as
> either mathematicians or physicists. The disciplines
> started acquiring more and more of their own disinct
> habits of thought.
>
> I wish I knew more about when and why this happened.
> For all I know, maybe it happened sometime around when
> mathematicians adopted the epsilon-delta definition of
> "limit". Physicists have never been particular fond of
> this: they still prefer to work with an intuitive version
> of infinitesimals.
Habits differentiate whenever a field gets so complex that
the majority of those shaping the field have difficulty
keeping up to date in the neighboring disciplines. At this
stage they generally use a compact version of that part of
the other field they need for progress in their own field,
and replace the deeper or more precise foundations by
shallow but intuitive substitutes, delegating the details
to those working in the other field.
This time-saving behavior works exceedingly well in most
disciplines, and becomes a barrier only when a field
develops in a way that deeper input from its neighbors
is needed again. But then the language and tradition has
changed already due to lack of regular communication,
and work from the other field becomes much more difficult
to assimilate. It becomes like other interdisciplinary work
- confined to the few who take the trouble to learn in depth
more than one field.
On the other hand, it also means that at the borderline
between two fields there are many of the most rewarding
questions, untouched or little explored because of the
inaccessibility of the problems to the 'typical' worker
in the field.
From my own experience (being primarily a mathematician
but having now about a dozen papers in computational physics),
the cultural differences between theoretical physics and
mathematics are significant, with exception of analytical
classical mechanics, which has a nice and elegant
mathematical structure.
In particular the fact that theoretical physicists
usually work from special cases to explain or infer
generalities makes it quite difficult for a mathematician
to understand scope and limits of concepts, and to
distinguish what is known with some reliability from
what is simply claimed by extrapolation from a few case
studies. Also, concepts are usually presented in some vague
form that need interpretation that is often only found by
reading between the lines.
My way of overcoming this barrier was to read the same
theme over and over again from as many perspectives as
I could find, until the common features emerged, and until
I found a paper or book that bothered to write down the
hints needed to make certain things clear.
On the other hand, for a physicist, the barrier to read
mathematics seems to lie primarily in the abstract
(and often poorly motivated) way mathematicians tend
to present their results in print, not so much in the
number of epsilons and deltas appearing in the text.
Arnold Neumaier
Mark
>the most impressive show of mathematical reasonment was the
>clasification theorem for regular solids. It was proved that there
>are five and only five (in three dimensions).
>As a consequence of this rigourous fact, the natural philosophers
>extended four elements with a new one, quintessence, so that they map
>naturally in the classification theorem. And this completely
>illogical step, muddly backed in mathematics, was the standard theory
>of matter for centuries.
You shouldn't be so hasty to judge. It is entirely possible, for
instance, that in some future theory the 4 phases of matter (solid,
liquid, gas, plasma) could be linked to the 5 exceptional finite
dimensional Lie algebras, with the 5th corresponding to a theretofore
unknown source of Dark Energy. The theory might even involve some kind
of duality transform which links the mathematical descriptions of many
body systems, relating plasma <-> solid phases, liquid <-> gas phases, with
the 5th item being self-dual.
Louis M. Pecora
<jeffery...@mail.com> wrote:
> Though not cited, it may have been Louis Pecora who wrote:
> > Please use high energy physics to explain how a car works. You
> > can't, and you shouldn't. The current interesting work in science
> > is not in the elucidation of single layers of explanation, but in
> > the connections between layers. Theory without experiment is just
> > as useless as observation without explanation.
> Are you claiming that explaining how a car works is of equivalent
> importance to explaining the Universe?
The car is part of the universe. A small part. If you can't explain
that, how can you explain the whole thing?
Peter Woit
John Baez wrote:
>Von Neumann
>and Wigner are among the few greats of the 20th century
>who defy being classified as either mathematicians or
>physicists.
>
>
Seems to me Wigner was pretty clearly a physicist and
von Neumann pretty clearly a mathematician. My own
vote for the twentieth-century figure who most
successfully straddled both fields (before Witten) would
be for Hermann Weyl.
the softrat
On 13 Oct 2003 00:14:56 -0400, jeffery...@mail.com (Jeffery)
wrote:
>
>Are you claiming that explaining how a car works is of equivalent
>importance to explaining the Universe?
>
>Jeffery Winkler
It's all one to my wife.
George D. Freeman IV
the softrat ==> Careful!
I have a hug and I know how to use it!
mailto:sof...@pobox.com
--
'Sarcasm: the last resort of modest and chaste-souled people
when the privacy of their soul is coarsely and intrusively
invaded' - Dostoevsky (after Paddy)
WEISS JEFFERY B
An interesting take on the Theory of Everything is an article by
Laughlin (1998 Physics Nobel Laureate) and Pines, (PNAS, v97,
n1, p28, 2000, http://www.pnas.org/cgi/content/full/97/1/28). Some
snippets:
"So the triumph of the reductionism of the Greeks is a pyrrhic
victory: We have succeeded in reducing all of ordinary physical
behavior to a simple, correct Theory of Everything only to discover
that it has revealed exactly nothing about many things of great
importance."
"The Josephson quantum is exact because of the principle of continuous
symmetry breaking. The quantum Hall effect is exact because of
localization. Neither of these things can be deduced from
microscopics, and both are transcendent, in that they would continue
to be true and to lead to exact results even if the Theory of
Everything were changed. Thus the existence of these effects is
profoundly important, for it shows us that for at least some
fundamental things in nature the Theory of Everything is irrelevant."
"Rather than a Theory of Everything we appear to face a hierarchy of
Theories of Things, each emerging from its parent and evolving into
its children as the energy scale is lowered. The end of reductionism
is, however, not the end of science, or even the end of theoretical
physics."
"The central task of theoretical physics in our time is no longer to
write down the ultimate equations but rather to catalogue and
understand emergent behavior in its many guises, including potentially
life itself. "
--
Jeffrey Weiss
jwe...@colorado.edu
Mark
Arnold Neumaier <Arnold....@univie.ac.at> writes:
>Habits differentiate whenever a field gets so complex that
>the majority of those shaping the field have difficulty
>keeping up to date in the neighboring disciplines.
The split in many cases is inessential and artificial. In the most
prominent example in differential geometry where you have what appear
to be two entirely different notations and languages, I've already
shown here in an earlier article how to easily bridge the two, for
instance, by a unified notation and language that is simultaneously a
superset of both the Physicists' index notation and Mathematician's
functional notation and naturally extends both sets into each others'.
Andrew Resnick
In <575262ce.03100...@posting.google.com> Jeffery wrote:
> Andrew Resnick <andy.r...@NOSPAM.grc.nasaDOTgov> wrote in message
> news:<20031006093...@newsread.grc.nasa.gov>...
>
>> antipathy felt towards the sciences by laypersons. Please use high
>> energy physics to explain how a car works. You can't, and you
>> shouldn't. The current interesting work in science is not in the
>> elucidation of single layers of explanation, but in the connections
>> between layers. Theory without experiment is just as useless as
>> observation without explanation.
>
> Are you claiming that explaining how a car works is of equivalent
> importance to explaining the Universe?
As a purely practical matter, I would argue that knowing how an
automobile works is of far more importance than explaining various
esoterica about the universe. Knowing how to replace the brakes, for
example. Or being able to perform simple road-side assistance. More
humorously, who makes more money- the factory certified mechanic or the
physics post-doc?
More seriously, I would again argue that the modern automobile is one of
the most complex pieces of machinery on the planet. And as far as
affordable pieces of machinery, possibly the *most* complex. There is a
circulatory system, a nervous system, a respiratory system, a digestion/
elimination system. The engine in itself is incredibly complex, never
mind the suspension system. And I'm leaving out all the computer
equipment that has to withstand living in the environment present on the
underside of a car.
And to reiterate another poster, how can you claim to understand or even
describe the universe if you can't explain how a car works? Or even more
simply, if you can't explain the interaction between the tire and the
road? Or the propagation of the flame front in a cylinder?
Physics is not just about inventing grandiose questions, but also of
finding the interesting problem in the most mundane of everyday things.
Arkadiusz Jadczyk
On Tue, 30 Sep 2003 05:47:20 +0000 (UTC), thomas_l...@hotmail.com
(Thomas Larsson) wrote:
>Here are some key quotes:
>
>Page 51, top left:
>
>"How can we ever hope to work in everyday practice with such entities
>as superstrings, parallel universes, wormholes, and phenomena that
>occurred before the Big Bang?
This is a good question. Do we know that for sure that these "entities"
are irrelevant for everyday practice? Is not the antrophic principle an
example of such an connection? And it does not matter whether the
principle is right or wrong, whether it is testable or not. If we have
one such principle, we will probably have similar, of the same kind. How
do we know that one of them will not revolutionize the whole of our
philosophy of science? And is there more important question than one:
how are things REALLY working? For science to make a progress, it must
not be bounded by any limits of practicality. Superstrings, parallel
universes, wormholes, and phenomena that occurred before the Big Bang?
Pretty abstract and probably will have to be replaced by other concepts,
and our questions will have to be refolmulated. But how can we learn how
to ride a bicycle without first falling off the bicycle a number of
times? We are probably approaching the next paradigm shift. Each time
the old paradigm crashes, it is painful, and each time it is more
painful than it was before - because the mountain of the "old knowledge"
is "higher". In the good old times we used to base our theories on
direct observations. Today rarely we deal with pure, original, data. We
deal with data that have been already processed by computers, when the
processing is based on assumptions and theories. If these theories will
have to be replaced by other theories, many of these data will have to
be reprocessed or discarded.
On the other hand chances are that physics, as it is now, will not make
any progress. It will come to a standstill, and there will be new
sciences that will grow. Biology, AI etc. But we do not know. The only
way to know is to give scientists FREEDOM to research any question they
want to research. So, the problem is rather whether WITHIN physics
the money for research is distributed reasonably. Perhaps too much goes
into fashionable domains and too little for supporting alternatives?
ark
--
Arkadiusz Jadczyk
http://www.cassiopaea.org/quantum_future/homepage.htm
--
Louis M. Pecora
<wo...@cpw.math.columbia.edu> wrote:
I think Wigner's PhD was in Chemical Engineering. The crossed over to
the 'dark side'. :-) That is an amazing jump. Still, I would
classifiy him as a physicist. The work I've seen pays close attention
to experimental results (the group theory work)even though it's very
theoretical -- but that theory is developed with a aim toward
calculation of measurable quantities in QM.
Louis M. Pecora
<jwe...@spot.colorado.edu> wrote:
> "The Josephson quantum is exact because of the principle of continuous
> symmetry breaking. The quantum Hall effect is exact because of
> localization. Neither of these things can be deduced from
> microscopics, and both are transcendent, in that they would continue
> to be true and to lead to exact results even if the Theory of
> Everything were changed. Thus the existence of these effects is
> profoundly important, for it shows us that for at least some
> fundamental things in nature the Theory of Everything is irrelevant."
I think Silvan Schweber made a similar statement in Physics Today (S.
S. Schweber, Physics Today (november 1993) p. 34) and he was also
quoting Anderson who expressed similar sentiments years before (P. W.
Anderson, Science {177}, 393 (1972) ). Schweber pointed to
Renormalization Theory (RT) as the foundation for these statements. I
wish I understood RT more to appreciate that.
I'm trying to recall from memory, but it seems the same as above.
Certain collective phenomena will be true regardless of some details.
Arnold Neumaier
Jeffery wrote:
>
> Andrew Resnick <andy.r...@NOSPAM.grc.nasaDOTgov> wrote in message
> news:<20031006093...@newsread.grc.nasa.gov>...
> > Please use high
> > energy physics to explain how a car works. You can't, and you
> > shouldn't.
> Are you claiming that explaining how a car works is of equivalent
> importance to explaining the Universe?
It is much more important. Not knowing how the universe works makes
little difference to modern society, not knowing how a car works would
create lots of difficulties...
Arnold Neumaier
Arnold Neumaier
>
> Arnold Neumaier <Arnold....@univie.ac.at> writes:
> >Habits differentiate whenever a field gets so complex that
> >the majority of those shaping the field have difficulty
> >keeping up to date in the neighboring disciplines.
>
> The split in many cases is inessential and artificial.
But it may take a lot of time to discover what is essential and natural,
time that must be spent by each researcher since the experts (heading
different traditions) do not agree.
> In the most
> prominent example in differential geometry where you have what appear
> to be two entirely different notations and languages, I've already
> shown here in an earlier article how to easily bridge the two, for
> instance, by a unified notation and language that is simultaneously a
> superset of both the Physicists' index notation and Mathematician's
> functional notation and naturally extends both sets into each others'.
The communication problem consists in that very few people use your
suggestion. So to read papers from one tradition if you were raised in
the other creates obstacles that take significant time to overcome.
Extending the notation creates a third tradition, but unless (and until)
that one dominates the problem persists.
Arnold Neumaier
Ralph E. Frost
"Thomas Larsson" <thomas_l...@hotmail.com> wrote in message
news:24a23f36.03100...@posting.google.com...
> dgo...@aol.com.bat.exe ( Doug Goncz ) wrote in message
news:<20031001091101...@mb-m22.aol.com>...
> > >From: thomas_l...@hotmail.com (Thomas Larsson)
> >
> > >Personally, I find it extremely disturbing that most physics
> > >professors, by their passivity, are allowing this paradigm shift to
> > >occur.
> >
> > Are they? Most? It only take one, not even a professor, to inititate a
paradigm
> > shift, right or wrong.
>
> I did not say that most particle physicists are doing things detached from
> experiments themselves. However, we all know that during the past 20
> years, a significant amount of work has been devoted to a field without
> experimental connection. Somebody has allowed this to happen.
>
> In a parallel thread, I recently pointed out that of string theory's main
> suggestions (not falsifyable predictions, because string theory does not
> deal in such old-fashioned notions), e.g. extra dimensions, supersymmetry,
> new gauge bosons, massless scalars associated with moduli, and a large and
> negative cosmological constant, *none* has been confirmed experimentally.
> The only reactions to this was that my observations were boring (Bergman)
> and premature (Motl). Is it really the consensus of the physics community
> that it is boring and premature to demand that some 20,000 man-years of
> taxpayer-financed work should result in some testable prediction?
>
> I also wonder how well known string theory's complete lack of experimental
> support is. Does the informed public know? Do most physicists know? Do
> grant and tenure committes know? And if they don't know, are they better
> off being kept in blissful ignorance?
The answer is, "no".
Minimally, hey should go on record as having been informed about the
difficulty and given the option to give teir informed consent. Or not.
This type of thing has all the makings of a Mayan Collapse if allowed to go
unchecked for too long.
--
Ralph Frost
Imagine a single internal analog language
made of ordered water...
and its variants.
http://flep.refrost.com
Mark
>The communication problem consists in that very few people use your
>suggestion. So to read papers from one tradition if you were raised in
>the other creates obstacles that take significant time to overcome.
>Extending the notation creates a third tradition, but unless (and until)
>that one dominates the problem persists.
None of this applies in this or any situation where C is simultaneously a
superset of A and B. Then everyone using A and B is ALREADY using C and has
already been raised in using C.
You forgot about that critical feature "simultaneous superset". It
doesn't create a third tradition, but zusammen-continues the other two.
Arnold Neumaier
> Arnold Neumaier <Arnold....@univie.ac.at> writes:
> >The communication problem consists in that very few people use your
> >suggestion. So to read papers from one tradition if you were raised
> >in the other creates obstacles that take significant time to
> >overcome. Extending the notation creates a third tradition, but
> >unless (and until) that one dominates the problem persists.
> None of this applies in this or any situation where C is
> simultaneously a superset of A and B. Then everyone using A and B
> is ALREADY using C and has already been raised in using C.
Only in using a subset of C. Therefore, this does not
necessarily help an A-person to read B-papers.
Knowing both traditions (or all three) but being used mainly
to A still creates a barrier to read B.
I learnt many formal languages representing various concepts
in math, computer science, physics, and chemistry,
with significantly overlapping concepts but different
terminology, but usually I find one of them much easier to
read than the others. In differential geometry, the physicist's
tradition is overladen with indices which makes reading slow,
while in stochastic processes it is the mathematician's tradition
that is much more adverse to easy reading than the physicist's
way.
Arnold Neumaier
From dae...@irje.ucar.edu Wed Oct 15 12:24:50 2003
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From: fii...@yahoo.com (Squark)
Newsgroups: sci.physics.research
Subject: Re: The Big Picture of Superstring Theory
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Aaron Bergman <aber...@physics.utexas.edu> wrote in message news:<abergman-095D94.20375114102003@localhost>...
> In article <939044f.03101...@posting.google.com>,
> fii...@yahoo.com (Squark) wrote:
> > Ok, so it seems to me M-theory is not unique (as usually
> > asserted), but at best labelled by space topologies and
> > asymptotic behavior at infinity.
>
> It would be nice to have an idea what M-theory is before making such
> blanket statements.
If we're not allowed making any kind of statements
about M-theory, we are not allowed to discuss what
M-theory "is" either. Nevertheless people do it
all the time.
> > Indeed, topology change
> > is unsupported by string theory as a manifold with topology
> > change admits no classical background.
>
> Certain types of singularities are completely unremarkable in the string
> theory moduli space. I don't know what you mean by a manifold with
> topology not admitting a classical background.
I mean that a manifold with non M x R topology
doesn't admit a metric which allows a foliation
by (possibly singular) spacelike hypersurfaces.
Possibly, though, that doesn't worry you as you
can do string theory on other kind of
backgrounds also. It is, however, unobvious
what kind of data is contained in such a string
theory and how to derive it.
> Blow up modes are easily identifiable. More interesting modes, too. The
> conifold transition seems to be completely smooth in nonperturbative
> string theory, also.
Interesting. How does it work?
Best regards,
Squark
------------------------------------------------------------------
Write to me using the following e-mail:
Skvark_N...@excite.exe
(just spell the particle name correctly and change the
extension in the obvious way)
holog
John Baez wrote:
> In article <BBAB5D42.25ECA%T...@timsilverman.demon.co.uk>,
> Tim S <T...@timsilverman.demon.co.uk> wrote:
>
>
>>on 8/10/03 7:25 am, John McCarthy at j...@Steam.Stanford.EDU wrote:
>
>
>>>Peter Shor wrote:
>
>
>>>>At the beginning of the last century (at least according to
>>>>some accounts I've read), a lot of physicists thought that
>>>>physics was mainly solved, with only a few theoretical
>>>>inconsistencies (such as the ultraviolet catastrophe).
>>>>These inconsistencies were actually hints that quantum
>>>>mechanics and relativity existed, which of course were both
>>>>major revolutions.
>
>
> "So far as astronomy is concerned, we must confess that we do
> appear to be fast approach the limits of our knowledge."
>
> So, there seems to be some truth to the idea that some people
> underestimated how much there was left to learn back in the late 1800s.
>
> .......................................................................
>
> References:
>
> Michelson quote:
> http://www.madsci.org/posts/archives/dec98/912518006.Sh.r.html
>
> other quotes, except for second quote by Maxwell:
> http://www.cccu.org/doclib/20020528_Sep00.pdf
>
>
>
>
>
>
>
I wonder how much of physics research is dependent on the technology at
hand.
Have we reached a limit of what we can see with todays technology?
Maybe we
have to go another step out in space to reach the next level of
understanding.
just a thought
holog
Robert J. Kolker
Arnold Neumaier wrote:
> On the other hand, for a physicist, the barrier to read
> mathematics seems to lie primarily in the abstract
> (and often poorly motivated) way mathematicians tend
> to present their results in print, not so much in the
> number of epsilons and deltas appearing in the text.
I speak as an amateur so do forgive me. It seems that mathematics has
come a long way from the days of Gauss who invented differential
geometry as a natural outgrowth of his map making endeavors. Physical
reality is rich with stucture and problems, surely more than enough to
fill the platters and cups of mathematicians.
A good deal of current mathematics is very derivative. It seems to draw
its life force from other mathematics, rather than from physical
reality. Am I mistaken in this assesment?
I fully sympathize with mathematicians who are seduced and enamoured of
abstract structure as such. It is beautiful. The sage Judah haLevy once
warned the faithful to beware of the tree of Greek learning for it
sprouts many beautiful flowers but bears little or no edible fruit.
Analagously, the blandisments of abstraction are such that the beauty
outshines concrete connection to reality. Beware of abstraction, which
flowers beautifully but bears little or no edible fruit.
Bob Kolker
Kevin A. Scaldeferri
>importance to explaining the Universe?
I don't know. Why don't you hold on while I go ask my neighbor...
--
======================================================================
Kevin Scaldeferri Calif. Institute of Technology
The INTJ's Prayer:
Lord keep me open to others' ideas, WRONG though they may be.
G.F. Thomas
>"Serenus Zeitblom" <serenusze...@yahoo.com> wrote in message
>news:c7fd6c7a.03100...@posting.google.com...
>[...]
> I strongly disagree with this. Science and Nature are basically
> biology journals these days, so the prominence of biology in
> their pages is not an occasion for surprise.
The physical sciences are well represented in Science and Nature and
in PNAS for that matter.
>
> And as for levels
> of scientific integrity --- well, look at the amazing amount of
> publicity given to the sequencing of the human genome: an
> "achievement" of no more real fundamental scientific significance
> than the sequencing of the porcupine genome.
>
Genome sequencing is of seminal scientific importance.
>
> Then again, look at
> the Proceedings of the National Academy of Sciences, a supposedly
> prestigious journal full of total bullshitlike mathematical
> economics.....
>
PNAS is a prestigious journal of the highest standards and
mathematical economics is is not nonsense.
>
>THE most important science of 2003 was the
> announcement of the WMAP data, which will not be published
> in Nature or Science.
>
The value of WMAP data is not in doubt. To claim that it's ' most
important science of 2003' is premature and subjective. Take a look at
Luminet et al., Nature 425, 593 - 595 (09 October 2003):"Dodecahedral
space topology as an explanation for weak wide-angle correlations in
the cosmic microwave background."
>And how many papers does Ed Witten have in the PNAS?
>
My guess is none so far but give it time.
--
Ciao,
Gerry T.
Arnold Neumaier
> We are probably approaching the next paradigm shift. Each time the
> old paradigm crashes, it is painful, and each time it is more
> painful than it was before - because the mountain of the "old
> knowledge" is "higher". In the good old times we used to base our
> theories on direct observations. Today rarely we deal with pure,
> original, data. We deal with data that have been already processed
> by computers, when the processing is based on assumptions and
> theories. If these theories will have to be replaced by other
> theories, many of these data will have to be reprocessed or
> discarded.
I don't think so. With every paradigm shift, the already established part
of science did not change much. Only the borderline cases that could not
be treated well with the old paradigms change a lot, and much new stuff
becomes accessible.
Thus the height of the mountain of knowledge is not the problem, but
only the parts that are still covered by fog. Getting them under control
once the way is discovered may well be less painful than studying string
theory.
Arnold Neumaier
Phillip Helbig---remove CLOTHES to reply
Pecora" <pec...@anvil.nrl.navy.mil> writes:
> > Seems to me Wigner was pretty clearly a physicist and
> > von Neumann pretty clearly a mathematician. My own
> > vote for the twentieth-century figure who most
> > successfully straddled both fields (before Witten) would
> > be for Hermann Weyl.
> I think Wigner's PhD was in Chemical Engineering. Then he crossed
> over to the 'dark side'. :-) That is an amazing jump.
I believe Witten was originally a historian: an even bigger jump.
Joe Rongen
Quoting Hermann Bondi in "Logical Foundations in Physics":
"In my own view, if one percent of the effort spent on physics were
devoted to clarification, we could soon teach the basic concepts of
quantum mechanics to the general run of nine-year-olds!"
Arnold Neumaier
>
> A good deal of current mathematics is very derivative.
> It seems to draw
> its life force from other mathematics, rather than from physical
> reality. Am I mistaken in this assesment?
It depends on the meaning given to 'a good deal'.
Of course many mathematicians work on problems inspired by
other mathematics, just as many physicsits work on problems
inspired by other physics. But the major part of the math
I see is inspired by applications, not only from physics
but from chamistry, biology, engineering, computer science,
artificial intelligence, finance, etc.
Physics is not the only science using mathematics, and apart from
physical reality there is also social reality (e.g. labor markets,
medical expert systems, or web searching) that require
sophisticated mathematical tools.
Arnold Neumaier
Starblade Darksquall
> Lubos Motl wrote:
> >
>
> > What I want to emphasize is that even in the current era, formal
> > mathematical rigor is a much cheaper value than physical depth and
> > consistency of the theories. One can rewrite a meaningless theory into a
> > precise language of axioms and theorems, but it won't make this theory
> > more meaningful.
>
> This is not what is meant with rigor. Rigor means deriving results
> without logical gaps, and this means for physics no ill-defined
> limits or asymptotic series without a well-defined recipe for making
> them produce exact numbers. From this point of view, practical quantum field
> theory is presently outside formal mathematical rigor.
>
> And it is much harder to make QFT rigorous than to pursue string
> theory at the traditional level of sloppiness. So what is cheaper???
>
> Arnold Neumaier
Are they still using perturbative models of QFT where the main
constructs are either particle or virtual particles? And where they
still have renormalization problems?
(...Starblade Riven Darksquall...)
Arnold Neumaier
rather, perhaps 19 year olds.
But I agree, theroetical physics is doing far too little
on didactical matters. Polishing what is already known (and make
it better understood that way) is valued much less than
speculating about new physics that hasn't been observed.
Arnold Neumaier
Arnold Neumaier
Starblade Darksquall wrote:
>
> > And it is much harder to make QFT rigorous than to pursue string
> > theory at the traditional level of sloppiness.
>
> constructs are either particle or virtual particles? And where they
> still have renormalization problems?
Renormalization problems are well understood and controlled for
gauge theories; only quantum gravity is a pariah here.
Perturbative calculations are the rule, but to compute
meson and Baryon spectra, other techniques (lattice gauge theory,
Bethe-Salpeter equations) are being used. However, these
are approximate, too, and a mathematically well-defined
conceptual basis is missing even for QED.
Arnold Neumaier
Philip M. Johnson
G.F. Thomas wrote:
> The physical sciences are well represented in Science and Nature and
> in PNAS for that matter.
I think I have to disagree with part of that statement. Science and
Nature do both represent the physical sciences well, but PNAS seems
to be largely a life sciences journal. Let's take a brief look
at the TOC of the most recent issue (Oct 14, 2003):
Commentaries: 4, all about the life sciences
Physical Sciences: 10 articles
Social Sciences: 2 articles
Biological Sciences: 89 articles
Granted, the Bio Sciences section does contain a "Biophysics"
section, but that doesn't anywhere near level the playing field.
Taking a quick glance at the other issues, these numbers
seem fairly typical.
--
Philip M. Johnson
p...@no.spam.physics.mun.ca
Mark
Peter Woit <wo...@cpw.math.columbia.edu> writes:
>John Baez wrote:
>>Von Neumann and Wigner are among the few greats of the 20th century
>>who defy being classified as either mathematicians or physicists.
>Seems to me Wigner was pretty clearly a physicist and
>von Neumann pretty clearly a mathematician.
Foreshortened perspective, since you're probably not aware of ALL of
what he was doing. von Neumann wrote in Mathematics, Quantum Physics,
Algebra, Computer Science. In fact, the von Neumann machine is the name
of the standard architecture underlying modern computing machines, in
contrast to a non-von Neumann machine such as cellular automata
(also originating from von Neumann).
robert bristow-johnson
on 10/24/2003 20:34:
> ... In fact, the von Neumann machine is the name
> of the standard architecture underlying modern computing machines, in
> contrast to a non-von Neumann machine such as cellular automata
> (also originating from von Neumann).
Another non-von Neumann architecture that might deserve mention is the
so-called "Harvard Architecture" that most DSP chips are designed to
be.
r b-j
G.F. Thomas
"Philip M. Johnson" <p...@no.spam.physics.mun.ca> wrote in message
news:bn38oo$hb3$1...@coranto.ucs.mun.ca...
> G.F. Thomas wrote:
Thank you for the comment. The figures you quote are typical and
reflect the current greater activity in the biological sciences over
the physical sciences. I'd be surprised if the playing field were
level but at least the physical sciences have not been shut out of
PNAS. I'll agree that PNAS is not the first recourse for frontier
physics but I've had many occasions to refer to it and, unlike a
previous poster's claim, I don't see PNAS as 'a supposedly prestigious
journal full of total bullshit'.
--
Ciao,
Gerry T.
John Baez
Robert J. Kolker <bobk...@attbi.com> wrote:
>A good deal of current mathematics is very derivative. It seems to draw
>its life force from other mathematics, rather than from physical
>reality. Am I mistaken in this assesment?
Lots of mathematics is inspired by other mathematics, but
especially in the last 10 years a lot of top-notch mathematics
has been inspired by physics. In this time the Fields medal has
been awarded to people including Kontsevich, Drinfeld, Borcherds,
Jones and Witten, all of whom were very much inspired by physics -
especially conformal field theory, integrable systems and string
theory. Indeed, most people consider Witten a physicist!
Of course, the irony is that these particular branches of
physics are in many ways more like mathematics than physics,
since they rely for their appeal mainly on intrinsic elegance
rather than successful prediction of experimental results.
>I fully sympathize with mathematicians who are seduced and enamoured of
>abstract structure as such. It is beautiful. The sage Judah haLevy once
>warned the faithful to beware of the tree of Greek learning for it
>sprouts many beautiful flowers but bears little or no edible fruit.
>Analogously, the blandisments of abstraction are such that the beauty
>outshines concrete connection to reality. Beware of abstraction, which
>flowers beautifully but bears little or no edible fruit.
It actually doesn't sound like you fully sympathize with these
mathematicians. If you did, you might point out that edible fruit
is mainly good because it keeps us alive and able to enjoy the
flowers. :-)
(Also, it tastes nice - another form of beauty.)
John Baez
Lubos Motl <mo...@feynman.harvard.edu> wrote:
>Someone invented the definitions (defining axioms) of groupoids, sheaves,
>categories and other things, and other mathematicians play with these
>notions - strictly within the pre-defined rules - without asking whether
>the definition is useful, good or appropriate.
Sorry, this is wrong. All these mathematical concepts were invented
in order to tackle specific problems which were frustrating the best
mathematicians of the day, and they caught on because they proved
effective in solving these problems - and a host of *other* problems
as well.
Maybe it's time for a little history lesson. Since I don't have
time to go over the history of groupoids, sheaves *and* categories
before breakfast, I'll just pick one.
Categories. Categories were invented in 1947 by Eilenberg and
Mac Lane in order to formalize the concept of a "natural"
construction - one not relying on arbitrary choices. At the
time, there was a bewildering variety of definitions of the
cohomology of a space. Simplicial cohomology as originally
invented by Poincare was good for spaces that were already
chopped up into simplices, but for other sorts of spaces it
was better to use other sorts of cohomology: singular cohomology,
Cech cohomology, de Rham cohomology and so on. In nice cases,
all these cohomology theories give the same answers... but
the question arose, what does "the same" mean?
It's not good enough to get isomorphic cohomology groups, since
one needs a *specific isomorphism* to relate the two theories
in a practical way. Moreover, to be really useful, this
isomorphism should be "natural" - not dependent on arbitrary
choices. But what does "not dependent on arbitrary choices"
mean, exactly? Eilenberg and Mac Lane invented the concepts
of category, functor and natural transformation to give 100%
precise answers to these questions.
After this, people could easily prove that naturally isomorphic
cohomology theories are really "the same" for all practical purposes,
and stop worrying about the proliferation of different theories.
Ever since, algebraic topology has made heavy and ever increasing
use of category theory. Key moments in this development were the
realization in 1952 that cohomology theories can be described purely
as functors satisfying a certain list of properties, the introduction
of abelian categories to provide a good foundation for homological
algebra, the recognition that simplicial sets and other simplicial
objects were functors from the category of simplices to other
categories, and the introduction of model categories by Quillen
in the 1960s to extend homological algebra to "homotopical" -
i.e. nonabelian - situations.
I will not try to describe how category theory became important
in algebraic geometry, starting with the work of Grothendieck.
Instead, I'll jump forwards to the late 1980s, when categories started
playing an important role in mathematical physics. This process
began with Graeme Segal's definition of a conformal field theory
as a functor satisfying a certain list of properties. Then came
Atiyah's similar definition of topological quantum field theory,
Moore and Seiberg's construction of "modular categories" from
conformal field theories, and the work by Witten, Reshetikhin,
Turaev and others to construct Chern-Simons theory from modular
categories consisting of representations of quantum groups.
One of the most important effects of this work for category theory
has been an upsurge in interest in braided monoidal categories,
and also n-categories.
All these developments in category theory occurred in response to
specific problems that the best mathematicians of the day were
struggling with. Any decent mathematician could tell you what a
bunch of those problems are. I'd be glad to do it if I had time.
But my point is this:
Quite contrary to the notion that mathematicians idly write down rules
and then blindly work within them, most of the above concepts underwent
significant optimization after they were first invented! The reason
is that these concepts are *tools*. As any machinist can tell you,
you have to fiddle around with tools to get them to work better.
For example, if you look back, you'll find considerable tinkering went
on before the definition of "abelian category" reached its current form -
with some variants like additive categories still being very handy at
times. And the definition of "model category" is still evolving as
we speak! Part of the reason is that people are putting it to ever
harder work - e.g. Voevodsky's proof of the Milnor conjecture, a big
puzzle in algebraic geometry, using methods of homotopical algebra.
Indeed, if you look at Hovey's recent book "Model Categories",
available for free here:
http://www.math.uiuc.edu/K-theory/0278/
you'll find that he proposes a new definition of the model categories,
designed to make it easier to work with several model categories at a
time.
Anyone who thinks that math is a game within preestablished rules would
be shocked to discover a definitive text on some subject changing the
definition that the subject is based on! But math is *not* about
games played within preestablished rules. Like physics and the other
sciences, math is a no-holds-barred struggle to understand the universe.
It's fun - but it's no game.
Lubos Motl
> Sorry, this is wrong. All these mathematical concepts were invented
> in order to tackle specific problems which were frustrating the best...
Your description is mostly an advertisement of category theory and more
generally the approach to mathematics that is sometimes called
"post-modern algebra" (this term comes from Ross Street); it is not quite
an accident that we encountered the same adjective that is also associated
with the people whose way of thinking was exposed by Alan Sokal, for
example.
A typical feature of post-modern methods is that various superficial
schemes are interpreted as the knowledge itself, without the emphasis on
investigation of the inner workings of the individual objects. The
independence of a specific representation is also the key aspect of
category theory: one only studies the relations of the *whole*
mathematical structure with the *exterior* objects, not the particular
internal structure.
Post-modern mathematicians are tired by "modern algebra" that "only"
analyzed the mathematical structures i.e. sets with operations and
relations. They want to put themselves one level or more levels higher.
Well, this is certainly a nice principle and an ambitious plan, but does
it really lead to something new? Is not the whole abstract language of
category theory equivalent to sentences of the form "it does not really
matter whether you imagine the structure XY to be made of AB or CD because
the rules will be identical"?
A post-modern anthropologist believes that she understands the rules and
the culture of the physicists if she is able to compare their behavior and
their verbal skills with the behavior of primitive tribes in the Pacific
Ocean. What about post-modern algebra?
In general terms, it is a rather easy philosophy that the same methods
should be applied to the methods themselves. Post-modern mathematicians
believe that this is the best way to make progress - and the most natural
way to extend mathematics. Well, it is certainly a controversial statement
- the progress in physics during the last 50 years was certainly done
differently. According to their approach, one should not be satisfied
with a discovery of homomorphisms: he should continue to try to look for
morphisms and structures connecting morphisms themselves, and so on, ad
infinitum. One should not be satisfied with a homotopy theory; we should
study homotopy of homotopies, homotopy of homotopies of homotopies, and so
on.
Note that this is a pretty specific strategy to make a progress. Among all
possible strategies, this is the fastest strategy to get disconnected from
reality. It is an approach in which we don't look inside to see the inner
structure; we look outside.
Well, John Baez is certainly right that the concept of category was
historically created in the context of cohomology theory, but he is
heavily exaggerating the importance of the language of category theory.
All the actual proofs that he uses as arguments in favor of category
theory included very specific constructions that didn't depend on the
concepts of category theory in an essential way. Category theory is just a
language - a language that most people don't understand although they
usually understand the simple ideas behind it (for example, the idea of
commutative diagrams). For example, the equivalence between the (my
fellow) Cech cohomology and de Rham cohomology was proved by Weil in 1949.
Good textbooks are able to present all these ideas without the meta-formal
terminology - I believe that this is even the case of Nakahara's book, for
example.
The fancy words such as "category" don't help almost anyone to understand
which transformations and constructions are natural and which are not. If
it were possible to completely formalize the rigorous meaning of the word
"natural" or "independent on arbitrary choices", people could not disagree
about the questions whether XY-theory of quantum gravity is
background-independent, mathematically rigid or not. You would just
present a mathematical proof. Obviously, it's not possible. The number of
various ways how the ideas and abstract concepts are related is large and
new ones are being discovered every year.
The case of different definitions of cohomology is completely trivial from
a conceptual point of view. Assuming that the manifold is nice and so on,
one can just calculate the same cohomology groups in different ways - and
identify the elements of the cohomology groups resulting from all these
(isomorphic) constructions. From a purely mathematical rigorous viewpoint,
the elements of the "different" cohomology groups are different objects -
equivalence classes of different objects with respect to different
relations and so on. From a physical point of view, everyone can imagine
something that is shared by an element of one cohomology and an element of
another cohomology - it's the thing that we call the cycle. It's just a
canonical "isomorphism", a uniquely defined relabeling or reinterpretation
of the same object into different languages.
It's great to know that various particular things can have many
representations that are isomorphic, but it is not great at all to insist
that the internal structure and the actual representation should not be
worked with! In order to compare our theories with reality - or even to
check whether they can exist in reality - one must *always* have *a*
representation. And without having the actual ensemble of different
representations, the fact that many of them may be isomorphic would be
meaningless.
> ... and they caught on because they proved ...
I apologize but this is sci.physics.research, and because this name of the
newsgroup contains the word "physics" and not "mathematics", let me just
emphasize the obvious fact that category theory, groupoids, Hopf
algebroids and all these things did NOT catch on in our field. At least so
far, they have not been essential for discoveries in physics and they
have not simplified physicists' life. This is why it has not become useful
for most physicists to learn these words.
> Categories. Categories were invented in 1947 by Eilenberg and ...
I am happy that you used the word "invented".
> Ever since, algebraic topology has made heavy and ever increasing
> use of category theory. Key moments in this development were the ...
Sorry but this whole description is just a fancy way to characterize
the things that can be explained in human language, too.
> Instead, I'll jump forwards to the late 1980s, when categories started
> playing an important role in mathematical physics. This process
> began with Graeme Segal's definition of a conformal field theory
At least superficially, this seems very unfair. A reader who would not
check what you're saying would think that these things were really
important for mathematical physics and physicists are working with them
often. Please open
http://www.slac.stanford.edu/spires/find/hep/www?rawcmd=find+a+segal%2Cg
You will learn that G. Segal became famous for his very explicit
construction of "unitary representations of some infinite-dimensional
groups" because this paper has about 350 citations.
As far as I can see, the texts that you describe as "important for
mathematical physics" - a definition of a CFT as a functor - have no
citations at all. Normally we would say that such texts, unlike the
article above, were not important for mathematical physics at all. Am I
missing something?
So far I am not able to find a note about the Atiyah's functor paper at
all.
It also don't seem that the other papers by the famous physicists are
really "category theory papers".
Could you please give me some more precise references that show more
clearly why you call the formal things "important for mathematical
physics" and why do you count the actual physics papers to be based on
category theory?
> Anyone who thinks that math is a game within preestablished rules would
> be shocked to discover a definitive text on some subject changing the
> definition that the subject is based on! But math is *not* about
> games played within preestablished rules. Like physics and the other
> sciences, math is a no-holds-barred struggle to understand the universe.
No, mathematics is not the same thing as physics. Mathematics is an
intelectual activity to understand the logical structures and patterns
that are independent of any particular observations, emotions or
experiences - i.e. of the things that we call the Universe. Mathematics is
precisely what you say that it's not: it's investigation of logical
consequences of pre-established rules. Some rules might be more
interesting to study than others - and certainly many mathematicians try
to choose the more interesting ones - but it does not change the fact that
mathematics is not a struggle to understand the universe, but an
investigation of logical structures that emerge from pre-established rules
that were defined by other mathematicians.
> It's fun - but it's no game.
It depends on the meaning of the word "game".
Let me end up with an example of ideas which find category theory useful:
some people want to describe consciousness and ethics with category theory
- and perhaps, it will also lead to quantization of gravity using the
"bundles of general ideas".
http://www.physics.helsinki.fi/~matpitka/articles/acategory.html
Do you think that it is science?
______________________________________________________________________________
E-mail: lu...@matfyz.cz fax: +1-617/496-0110 Web: http://lumo.matfyz.cz/
phone: work: +1-617/496-8199 home: +1-617/868-4487
^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^
Superstring/M-theory is the language in which God wrote the world.
A.J. Tolland
On Sat, 8 Nov 2003, Lubos Motl wrote:
> Your description is mostly an advertisement of category theory and more
> generally the approach to mathematics that is sometimes called
> "post-modern algebra" (this term comes from Ross Street); it is not quite
> an accident that we encountered the same adjective that is also associated
> with the people whose way of thinking was exposed by Alan Sokal, for
> example.
"Not quite an accident"? Ross Street's description was a joke,
and your analogy is an attempt to create guilt by association, a
rhetorical trick so clumsy it's funny. The best part is that by
(deliberately?) misinterpreting Street's comment, you engage in the same
sort of nonsensical reasoning that Sokal was satirizing!
Your post is a bit too long to respond to in detail, so let me hit
a few of the key bits.
> Category theory is just a language - a language that most people don't
> understand although they usually understand the simple ideas behind it
Yes, category theory is 'just' a language. So is English. I
presume you would not advocate a return to Indo-European, so it puzzles me
that you're so vehemently against the use of categorical terminology.
It's not that difficult: If you understand the simple ideas behind
category theory, you understand category theory.
And it's quite useful. Category theory may not be essential for
elementary algebraic topology, but it's nearly indispensible for more
advanced topics in algebraic geometry, algebraic topology, and
representation theory. Yes, it's possible to discuss the technical
details of, for instance, moduli spaces, gerbes, elliptic cohomology, and
vertex algebras without ever saying the word "functor", but it's pointless
to do so. (Unless, like Georges Perec and Gilbert Adair, you take
pleasure in doing things the hard way.)
The point is, category theory uses external relations (like set
injections and ring homomorphisms) to isolate essential internal structure
(like subsets and ideals). As JB said, this approach has proven itself
useful to mathematicians over the past 40 years. I'm willing to bet that,
as theoretical physicists spend more time with mathematics, they will find
themselves adopting this terminology as well.
Sometimes I think we could use category theory as a test to
determine when someone is really a mathematical physicist. Of course, we
would probably need S-matrix computation to tell when someone is really a
theoretical physicst.
> http://www.slac.stanford.edu/spires/find/hep/www?rawcmd=find+a+segal%2Cg
>
> You will learn that G. Segal became famous for his very explicit
> construction of "unitary representations of some infinite-dimensional
> groups" because this paper has about 350 citations.
Segal has been famous since the late 60's. The paper you refer to
was published in 1981. And while we're on the subject, Segal's fame is
not a function of the number of citations he's landed. In fact, it's
often difficult to cite Segal, because he's only written down a fraction
of the good ideas he's given to mathematical physics.
His paper on conformal field theory is particularly notorious in
this regard. It's been circulating by photocopied preprint for about 15
years.
> Mathematics is precisely what you say that it's not: it's investigation
> of logical consequences of pre-established rules.
Uhuh. And physics is solving equations and writing down numbers
that come from a detector. Has it occured to you that most of the art in
mathematics (as in physics) lies in choosing what to study and how to
think about it? This is why Eilenberg and MacLane are respected for
_inventing_ categories.
--A.J.
Lubos Motl
> ... rhetorical trick so clumsy it's funny. The best part is that by
> (deliberately?) misinterpreting Street's comment, you engage in the same
> sort of nonsensical reasoning that Sokal was satirizing!
OK, I accept this criticism. At least we can be happy that we agree that
Sokal was - more or less - right.
> Yes, category theory is 'just' a language. So is English. I
> presume you would not advocate a return to Indo-European,
Your assumption is not correct ;-) as the folks who've heard about my
intermittent problems with contemporary real English know very well haha,
but further discussion about this issue should probably be moved
elsewhere. I would endorse a global return to Latin - and perhaps even old
Indo-European, although I have not tried to learn this language. Does
someone know how this language looked like? The world would also benefit
if everyone learned Czech! Well, six years ago the bureaucrats at Rutgers
rejected my master diploma from Prague because it was written in Latin! :-)
You know, I admire America, but such experiences reinforce the vague idea
about Americans being uncultural.
Let's put our language preferences aside because I believe that the
comparison of good and bad formalisms and theories in mathematics is much
sharper and must be much sharper than the differences between English and
Latin, for example.
> so it puzzles me that you're so vehemently against the use of
> categorical terminology. It's not that difficult: If you understand
> the simple ideas behind category theory, you understand category
> theory.
I don't think so. Please try to understand that some people feel some
discomfort if they hear simple ideas hidden into unreasonably fancy
terminology. (The opposite extreme is also bad. The language should not be
oversimplified because it would become ambiguous.) Natural selection has
not trained our species to describe the ideas covered by category theory -
the ideas that even appear in everyday life - by such abstract
terminology.
> representation theory. Yes, it's possible to discuss the technical
> details of, for instance, moduli spaces, gerbes, elliptic cohomology, and
> vertex algebras without ever saying the word "functor", but it's pointless
> to do so.
Many people in our field have adopted the mathematical terminology and the
mathematical way of thinking about these things - including a lot of
nontrivial knowledge - but let me express a satisfaction with the fact
that at least functors have not joined the family of gerbes and bundles so
far. A physicist who would start to use the word "functor" too often would
hopefully be removed by natural selection. ;-)
> useful to mathematicians over the past 40 years. I'm willing to bet that,
> as theoretical physicists spend more time with mathematics, they will find
> themselves adopting this terminology as well.
If string theorists are going to spend a significant portion of their time
with category theory, I will fully support the proposals to move them from
physics departments to mathematics departments. So far, such a phase
transition - fortunately - has not really happened. String theory is an
extremely physical theory and it makes us think about the problems in a
very physical way.
> Sometimes I think we could use category theory as a test to
> determine when someone is really a mathematical physicist. Of course, we
> would probably need S-matrix computation to tell when someone is really a
> theoretical physicst.
I would probably agree with this description. A mathematical physicist
defined above should probably be paid by a mathematics department.
> Segal has been famous since the late 60's. The paper you refer to
> was published in 1981. And while we're on the subject, Segal's fame is
> not a function of the number of citations he's landed. In fact, it's
> often difficult to cite Segal, because he's only written down a fraction
> of the good ideas he's given to mathematical physics.
Understood.
> > Mathematics is precisely what you say that it's not: it's investigation
> > of logical consequences of pre-established rules.
>
> Uhuh. And physics is solving equations and writing down numbers
> that come from a detector. Has it occured to you that most of the art in
> mathematics (as in physics) lies in choosing what to study and how to
> think about it?
Yes, surprisingly, it has occured to me ;-), but this fact describes a
strategy to choose problems, not the ultimate procedure of solving them or
the goal of the field. So let me reiterate that mathematics is
investigation of logical consequences of pre-established rules while
physics is about understanding the results of experiments using
mathematical tools.
> This is why Eilenberg and MacLane are respected for _inventing_
> categories.
Right. This is also why they're not respected as physicists. If someone
*invents* something, he can only be respected as a physicist if his
invention leads to some testable insights.
Arnold Neumaier
Lubos Motl wrote:
>
> On 9 Nov 2003, A.J. Tolland wrote:
>
> > Sometimes I think we could use category theory as a test to
> > determine when someone is really a mathematical physicist. Of course, we
> > would probably need S-matrix computation to tell when someone is really a
> > theoretical physicst.
>
> I would probably agree with this description. A mathematical physicist
> defined above should probably be paid by a mathematics department.
>
> So let me reiterate that mathematics is
> investigation of logical consequences of pre-established rules while
> physics is about understanding the results of experiments using
> mathematical tools.
Then string theory is neither mathematics nor physics.
It is too ill-defined to count as mathematics (hopes and 'formal'
arguments replace logically valid proofs) and too little
developed to make contact with experiment, hence fails the
test for physics, too.
Following your above argument, a string theorist should probably
be paid neither by a mathematics department nor by a physics
department!?
Arnold Neumaier
Lubos Motl
> Then string theory is neither mathematics nor physics.
> It is too ill-defined to count as mathematics (hopes and 'formal'
> arguments replace logically valid proofs) and too little
> developed to make contact with experiment, hence fails the
> test for physics, too.
String theory makes profound contributions both to mathematics and
physics. I thought that the experiment proving string theory is already
generally known.
> Following your above argument, a string theorist should probably
> be paid neither by a mathematics department nor by a physics
> department!?
You have made two errors in your reasoning. Yes, many string theorists are
paid by *both* departments.
Aaron Bergman
<Pine.LNX.4.31.03110...@feynman.harvard.edu>,
Lubos Motl <mo...@feynman.harvard.edu> wrote:
> At least superficially, this seems very unfair. A reader who would not
> check what you're saying would think that these things were really
> important for mathematical physics and physicists are working with them
> often. Please open
>
> http://www.slac.stanford.edu/spires/find/hep/www?rawcmd=find+a+segal%2Cg
>
> You will learn that G. Segal became famous for his very explicit
> construction of "unitary representations of some infinite-dimensional
> groups" because this paper has about 350 citations.
>
> As far as I can see, the texts that you describe as "important for
> mathematical physics" - a definition of a CFT as a functor - have no
> citations at all. Normally we would say that such texts, unlike the
> article above, were not important for mathematical physics at all. Am I
> missing something?
Yeah. SPIRES doesn't do math cites. Mathscinet gives 11 cites and I have
no idea how extensive its database is. For an unpublished work, it's
pretty widely known. I wouldn't discount it at all. I certainly wouldn't
discount the influence of Segal.
Aaron
Peter Woit
>Your description is mostly an advertisement of category theory and more
>generally the approach to mathematics that is sometimes called
>"post-modern algebra" (this term comes from Ross Street); it is not quite
>an accident that we encountered the same adjective that is also associated
>with the people whose way of thinking was exposed by Alan Sokal, for
>example.
>
>
>
During the 15 years I've spent in the math community, I've never heard
anyone
refer to "post-modern algebra", but I've heard many people refer to
string/M-theory as "post-modern physics". Many physicists have also
noticed the similarities between the excesses in the humanities exposed
by Sokal and the incoherent, fashion-driven speculative excesses that
now dominate
particle theory.
>The fancy words such as "category" don't help almost anyone to understand
>which transformations and constructions are natural and which are not. If
>it were possible to completely formalize the rigorous meaning of the word
>"natural" or "independent on arbitrary choices", people could not disagree
>about the questions whether XY-theory of quantum gravity is
>background-independent, mathematically rigid or not. You would just
>present a mathematical proof. Obviously, it's not possible. The number of
>various ways how the ideas and abstract concepts are related is large and
>new ones are being discovered every year.
>
>
>
"Fancy words" such as "category" aren't supposed to explain to you which
constructions are natural and which are not. They are meant to provide
a precise meaning to the vague notion of "natural", a precise meaning
that may or may not be appropriate, but at least you know what it is.
When a mathematician
tells you that a transformation is "natural", if you know a little bit of
category theory you know exactly what he is saying. When an M-theorist
like Lubos Motl tells you that a transformation is "natural", about all you
know is that it makes him feel good and undoubtedly has something to
do with how wonderful string theory is.
Many M-theorists are practicing a "post-modern" sort of physics in which
one never has to say exactly what one means, and can get away
with having no idea of what exactly one is talking about. This is one
big reason the field is going absolutely nowhere. Attacking mathematical
physicists for using precise language is not going to help matters. At
least
Witten realizes that these days the "M" is for "Murky".
>The case of different definitions of cohomology is completely trivial from
>a conceptual point of view. Assuming that the manifold is nice and so on,
>one can just calculate the same cohomology groups in different ways - and
>identify the elements of the cohomology groups resulting from all these
>(isomorphic) constructions. From a purely mathematical rigorous viewpoint,
>the elements of the "different" cohomology groups are different objects -
>equivalence classes of different objects with respect to different
>relations and so on. From a physical point of view, everyone can imagine
>something that is shared by an element of one cohomology and an element of
>another cohomology - it's the thing that we call the cycle. It's just a
>canonical "isomorphism", a uniquely defined relabeling or reinterpretation
>of the same object into different languages.
>
>
>
You give the strong impression here that you are unaware of the fact
that the
cohomology of finite-dimensional, smooth, compact manifolds with real
coefficients is only one of a huge array of cohomology theories and that
this is why you think that a natural language for expressing the properties
of a cohomology theory is "fancy words" that no one needs to really know.
A few examples of very different cohomology theories include:
Equivariant cohomology
Group cohomology
Hochshild cohomology
Lie algebra cohomology
Intersection cohomology
Cyclic cohomology
Cohomology of coherent sheaves
Galois cohomology
l-adic cohomology
motivic cohomology
and this is not even getting into generalized cohomology theories
such as K-theory and elliptic cohomology, where the language of
category theory really comes into its own. Some of these theories
are useful for studying mathematical objects that appear in physics,
some aren't, but anyone who wants to learn about these things and
how they are related to each other has to learn a few "fancy
words".
>>Instead, I'll jump forwards to the late 1980s, when categories started
>>playing an important role in mathematical physics. This process
>>began with Graeme Segal's definition of a conformal field theory
>>
>>
>
>At least superficially, this seems very unfair. A reader who would not
>check what you're saying would think that these things were really
>important for mathematical physics and physicists are working with them
>often. Please open
>
> http://www.slac.stanford.edu/spires/find/hep/www?rawcmd=find+a+segal%2Cg
>
>You will learn that G. Segal became famous for his very explicit
>construction of "unitary representations of some infinite-dimensional
>groups" because this paper has about 350 citations.
>
>
The idea that the number of citations of a paper in SPIRES is the way
to determine the significance of the ideas in the paper is the kind of
thinking
that has turned particle theory into a failing subject driven purely by
fashion and incapable of generating new ideas. For some historical
perspective, try this SPIRES search:
FIND C NUPHA,22,579 and date before 1971
and you'll learn what every hot-shot young physicist
working on the hot idea of the time in 1971 (string theory)
would have told you about this paper that tried to
use gauge theory to unify the weak and electro-magnetic
interactions. Clearly worthless since it was ten years old and Shelly
"string theory is a tumor on physics" Glashow hadn't gotten a
single citation for it.
Arnold Neumaier
>
> On 9 Nov 2003, A.J. Tolland wrote:
>
> > Sometimes I think we could use category theory as a test to
> > determine when someone is really a mathematical physicist. Of course, we
> > would probably need S-matrix computation to tell when someone is really a
> > theoretical physicst.
>
> I would probably agree with this description. A mathematical physicist
> defined above should probably be paid by a mathematics department.
>
> So let me reiterate that mathematics is
> investigation of logical consequences of pre-established rules while
> physics is about understanding the results of experiments using
> mathematical tools.
Then string theory is neither mathematics nor physics.
It is too ill-defined to count as mathematics (hopes and 'formal'
arguments replace logically valid proofs) and too little
developed to make contact with experiment, hence fails the
test for physics, too.
Following your above argument, a string theorist should probably
be paid neither by a mathematics department nor by a physics
department!?
Arnold Neumaier
Andrew Resnick
Motl wrote:
> String theory makes profound contributions both to mathematics and
> physics. I thought that the experiment proving string theory is
> already generally known.
>
<snip>
This is certainly news to me! Please elaborate on this experiment.
Parenthetically, experiments do not 'prove' physics theories, but can
discredit poor conjectures.
--
Andrew Resnick, Ph. D.
National Center for Microgravity Research
NASA Glenn Research Center
Lubos Motl
> This is certainly news to me! Please elaborate on this experiment.
We usually take a pen and let it freely fall. This experiment shows that
gravity exists in the real world. If one combines this experiment with
other experiments that show that our world is quantum, we see that our
world must unify quantum and gravitational phenomena. According to
everything we know today, it implies that the right theory then must be
string/M-theory because it is the only known (but probably the only
existing) theory that can achieve this task.
> Parenthetically, experiments do not 'prove' physics theories, but can
> discredit poor conjectures.
I would prefer Amanda Peet's description from PBS - the experiments can't
prove that your theory is correct; they can only prove that it is the best
theory you have. Well, this is what I did with string theory and the
experiment whose budget was less than 1 dollar. ;-)
Andrew Resnick
> On 12 Nov 2003, Andrew Resnick wrote:
>
>> This is certainly news to me! Please elaborate on this experiment.
>
> We usually take a pen and let it freely fall. This experiment shows
> that gravity exists in the real world.
A minor quibble- strictly speaking that's not true, but never mind for
now.
> If one combines this experiment
> with other experiments that show that our world is quantum, we see
> that our world must unify quantum and gravitational phenomena.
Well, this is not really true either- it's a belief. The world "must"
not do anything. Nature does what it will. It is our job as scientists
to understand what is given to us by patient observation. One must be
exceedingly careful when superposing one's beliefs with the
interpretation of measurements.
> According to everything we know today, it implies that the right
> theory then must be string/M-theory because it is the only known (but
> probably the only existing) theory that can achieve this task.
So in fact you have no experiment "Proving string/M-theory is correct".
Certainly no experiment contradicting string/M-theory, but that is a
different beast.
>
>> Parenthetically, experiments do not 'prove' physics theories, but can
>> discredit poor conjectures.
>
> I would prefer Amanda Peet's description from PBS - the experiments
> can't prove that your theory is correct; they can only prove that it
> is the best theory you have. Well, this is what I did with string
> theory and the experiment whose budget was less than 1 dollar. ;-)
That's a horrible description, and implies science is conceptually no
different from religion. Great science will isolate a single particular
facet of nature that is manifested in many, many physical systems of
interest- Joule's experiment on the equivalency of heat and work, Tycho
Brahe's observations of the night sky, use of the Ising model to
elucidate critical phenomena.
Arun Gupta
Lubos Motl <mo...@feynman.harvard.edu> wrote in message
> We usually take a pen and let it freely fall. This experiment shows that
> gravity exists in the real world. If one combines this experiment with
> other experiments that show that our world is quantum, we see that our
> world must unify quantum and gravitational phenomena. According to
> everything we know today, it implies that the right theory then must be
> string/M-theory because it is the only known (but probably the only
> existing) theory that can achieve this task.
> I would prefer Amanda Peet's description from PBS - the experiments can't
> prove that your theory is correct; they can only prove that it is the best
> theory you have. Well, this is what I did with string theory and the
> experiment whose budget was less than 1 dollar. ;-)
Very nice 1 dollar experiment :-)
I suppose you're saying that the pen falling shows that gravity exists;
and string/M-Theory has gravity in it.
Let us take this interpretation of this Galileo-like experiment as it is.
The problem is that while you have gravity in string theory, I have severe
doubts that you have the pen in the theory :-). (The pen is an object in
the Standard Model.)
Lubos Motl
On Fri, 14 Nov 2003, Arun Gupta wrote:
> Let us take this interpretation of this Galileo-like experiment as it is.
> The problem is that while you have gravity in string theory, I have severe
> doubts that you have the pen in the theory :-). (The pen is an object in
> the Standard Model.)
Of course that we have pens, or at least something that can be called
pens. Let me also say that many of us also study backgrounds of string
theory which don't contain pens, at least not the four-dimensional ones. :-)
String theory is a unifying theory, and therefore it must always
contain extra forces and matter, not only gravity.
There are many known vacua that describe unrealistic physics - for example
even the spacetime dimension can be different from four - and there are
some models with realistic matter contents.
There are several basic groups of nearly realistic scenarios - with
thousands of concrete models - how string theory reproduces the Standard
Model. Gravity is always a part of the picture.
1. The most conventional one (from 1985) - one that is still treated most
seriously by many string theorists including me - is heterotic string
theory (that has the E8 x E8 gauge group in 10 dimensions; it is a sort
of mixture of superstring theory and the old bosonic string theory, and
it was discovered by Gross, Rohm, Harvey, and Martinec) compactified
on a six-dimensional Calabi-Yau space (also called Calabi-Yau three-fold,
where 3 is the complex dimension); this realistic compactification was
discovered by Strominger, Witten, Candelas, and Horowitz. In the realistic
models, one of the E8 gauge groups is broken to a Grand Unified Theory
group - such as SO(10) or E6 - which is subsequently broken to the
Standard Model's SU(3) x SU(2) x U(1). Usually we are looking for the N=1
supersymmetric extensions of these theories, assuming that SUSY is broken
spontaneously.
One gets the correct spectrum of gauge bosons as well as fermions (perhaps
with the right-handed neutrino included, and in the E6 case some extra
fermions that complete the 27 representation of E6). One can also
calculate the number of generations. It can be 3, but it can also be
larger or smaller.
2. If the model above has a coupling constant that is stabilized around a
large value, a new 11th dimension of M-theory emerges. Because we started
with the heterotic theory, the new 11th dimension will have two
boundaries, each of them carrying a single gauge group E8, as was found by
Horava and Witten (therefore: "Horava-Witten theory" or "heterotic
M-theory"). This extra 11th dimension can be in fact much larger than the
6 dimensions of the Calabi-Yau space, and therefore the world would appear
as five-dimensional.
The scenarios 1,2 are conventional. Gravity becomes a quantum force at a
very large energy scale that is not directly accessible experimentally.
3. M-theory (the 11-dimensional theory) can also be directly compactified
to 7-dimensional manifolds. They must have a G2 holonomy to get N=1
supersymmetry in four dimensions, and they must contain singularity if we
want to reproduce the spectrum of chiral fermions. Interesting
calculations in these models exist - about the proton decay, for example -
and this model is in some sense the most geometrical one, because all the
extra stringy degrees of freedom beyond the visible 4 dimensions are
treated geometrically.
Fluxes - generalizations of the magnetic flux - are being added to the
previous models, and it leads to new useful physical features.
I am slowly approaching the braneworld scenarios that can have shocking
experimental consequences for the experiments that will be done before
2010: the braneworld scenarios allow the fundamental length/energy scale
to be nearby.
4. F-theory (by Cumrun Vafa, 1995) is formally a 12-dimensional theory,
but one must always compactify two of its dimensions on a two-torus, which
effectively leads to type IIB string theory. F-theory on a
(d+2)-dimensional manifold M is a fancy way to describe a compactification
of type IIB strings on a d-dimensional manifold which is the base of the
(d+2)-dimensional manifold M; the fiber must be a two-torus. The shape of
the two-torus determines the complex coupling constant of type IIB string
theory. F-theory on eliptically fibered (=the fiber is a two-torus)
Calabi-Yau four-folds (eight-dimensional ones) is a realistic theory again
because it leads to N=1 supersymmetry in four dimensions. Randall-Sundrum
models have been constructed using these models, for example.
5. Intersecting brane models (the present) often construct
non-supersymmetric Standard Models with essentially the right spectrum.
These particles are vibrating strings whose two ends are attached to
different D-branes that intersect. Various particles are therefore forced
to be localized at different intersections. These models can again be
realistic, and they naturally lead to hierarchy of fermionic masses.
Best wishes
Lubos
Danny Ross Lunsford
> We usually take a pen and let it freely fall. This experiment shows that
> gravity exists in the real world. If one combines this experiment with
> other experiments that show that our world is quantum, we see that our
> world must unify quantum and gravitational phenomena. According to
> everything we know today, it implies that the right theory then must be
> string/M-theory because it is the only known (but probably the only
> existing) theory that can achieve this task.
It isn't at all clear to me that gravity has to work like, say, a silver
atom. There is so little in common between systems that exhibit the
characteristic phenomena of quantization (superposition, spontaneous
emission, spin and spatial quantization) and those of gravity (curvature,
equivalence principle), and so little in common with the underlying
structures (Hilbert space vs. Riemannian geometry), that, on this surface,
your statement is sophistry. Explain to me in detail why a falling pen and
the Stern-Gerlach experiment force one to the conclusion that gravity is a
typical quantized system. Then explain to me how one can prepare an
experimental setup for measuring curvature, and how the superposition
principle applies. Then use this latter to explain what "quantum cosmology"
means.
--
-drl