On Getting Creative Ideas


Uploaded by Google on 24.07.2007

Transcript:

MALE SPEAKER: Hi, everyone.
Thank you for coming today.
It's my great pleasure to introduce one of the great
minds of our time, Murray Gell-Mann.
Professor Gell-Mann has a list of accomplishments so long
that I could spend all hour up here, reciting them.
I won't do that, but I'll highlight a few.
He's been recognized by the Atomic Energy Commission, the
Franklin Institute, the National Academy of Sciences,
the United Nations.
He has honorary degrees from, well, more institutions than
most of us have even attended.
And then there's that little prize he one in 1969, the
Nobel Prize.
He spent his life contributing to our understanding of the
world and the universe.
Today he's here to deliver a talk on
getting creative ideas.
So please join me in welcoming professor Gell-Mann.

MURRAY GELL-MANN: I'm very pleased to be here and to talk
with you about this subject.
Probably most of you heard most of the things that I'll
refer to, but maybe for each of you, there will be a little
nugget that's new.
I hope so.

The notion of a creative idea can be extended from science,
to art, and business, and many other
activities in which we engage.
And whenever a comparison is made among the different kinds
of applications, it seems that there
are very close parallels.
I was part of a group that met in an Aspen in 1969 to talk
about the experience of getting a creative idea, the
light bulb turning on, the aha!
moment.
And there was a poet, two painters, a theoretical
biologist, and I was the theoretical physicist. There
was another visual artist, a very famous one,
but he didn't stay.
He couldn't stand listening to anyone else talk.
And he went out and got drunk instead of staying.

That doesn't stop me from collecting his prints.
Anyway, all of us who spoke had very similar experiences.
There was a contradiction between certain established
are available ways of doing things and something we needed
to accomplish--
in art, the expression of a feeling of thought and
insight, in theoretical science, the explanation of
some observations.

Well, first of all, each of us worked for days or weeks or
months to resolve this contradiction between what was
needed and what we had, filling the
mind with the problem.

Then, second, there came a time when further conscious
thought seemed to be useless.
But somehow, outside of conscious awareness, mental
activity went on anyway, or at least that's my interpretation
of what happened.

Third, one day while cycling, or cooking, or shaving, or by
a slip of the tongue, while talking, or even while
sleeping and dreaming, according to some people, the
crucial idea turned up, that got us out of the rut, and
resolved the contradiction.
All of us at that meeting were impressed with the congruence
of our stories.
I discovered later, by reading, that
none of this was new.
The great German scientist, Helmholtz, in the late 19th
century, had already described three steps, and named them
saturation, incubation, and illumination, just
corresponding to what we were discussing.
Henri Poincare, the great mathematician, in 1908, added
a fourth step, obvious, but also crucial, verification.
Check that the idea works.

It turned out that the psychologist, Graham Wallace,
in his text in 1926, had already
listed these four steps.
But none of us knew about it.
None of us had read his book.

We just came across the same ideas through personal
experience, these four stages.

In theoretical science, a new idea may permit us to alter or
extend the body of theory to explain observations that
previously couldn't be understood, and, of course, to
make new predictions that can someday be verified.

Let me give an example from my own experience.
In fact, I'll give, a little later, another example for my
own experience.
But this one is earlier, 1952.
So-called strange particles have been observed in the
cosmic radiation.
Later on, they were observed also in accelerators when the
more energetic accelerators went online.

Some of us were trying to explain why these strange
particles took so long to disintegrate into other
particles, when they were made copiously.
If they were made copiously, they must
have interacted strongly.
But if they took a long time to decay, as much as one 10
millionth of a second, which in particle physics,
is a very long time.
They take a very long time to decay, they
must be weakly coupled.
So what was going on?
Well I thought I had succeeded in explaining this strange
behavior of the strange particles.
Let's take for example, a proton, a particle similar to
the neutron and proton, which was strange.
It was produced copiously, but took a long time to decay.

My attempt at explanation involves a quantity i,
isotopic spin.
i can have value 0, or 1/2, or 1, or 3/2, or whatever.
The conventional wisdom was that particles like the
neutron and proton, which have spin angular momentum 1/2, j
equals 1/2, had to have i equal 1/2, or 3/2, or 5/2, but
not an integer, not a whole number.
Other particles, mesons, with spin angular momentum j equals
0 would have i equals 0 or 1, or 2, or something, that would
be the similarity between the values of i and
the values of j.
It was a very nice idea.

But there was no reason for it.

I visited the Institute for Advanced Study, where I had
spent the previous year.
And people had heard that I had had an idea to explain the
strange behavior of a particular particle.

But then I realized that it wouldn't work.
I thought I had by assigning the value i equals 5/2 to this
particle that would prevent it from disintegrating, by means
of the strong interaction, into two particles with i
equals 1/2, and i equals 1, because with 1/2 and 1, you
can't seem to make 5/2.
However, it turned out that electromagnetism can change
this value of i by a half unit.
An electromagnetism isn't all that weak.
So the idea failed.
And the people at the Princeton Institute for
Advanced Study had heard that I had had an idea, but that it
hadn't worked.
And they asked me to explain the idea,
and why it was wrong.
Well, I got up to do so, and I said what I
had been saying here.
And when I got to this idea of assigning to the new particle
i equals 5/2, so it couldn't decay into 1 and 1/2, I made a
mistake, a slip of the tongue.
I said, i equals 1, instead of i equals 5/2.
I said, let's assign this particle i equals 1.
And then I stopped dead, because the electromagnetism
is going to change i by a half unit.
So if it really had i equals 1, that
would solve the problem.

But everybody thought that this particle had to have half
integral values of i.
Well I quickly reviewed in my mind what could be the reason
for this prohibition.
And then I realized there wasn't any reason.
It was just something that people told one another.

It didn't take long.
It just took a few, half a minute or something, for me to
realize that there was no reason for this rule.
And I can freely violate it.

So the rest of the seminar was quite different from what was
anticipated.

Here it is written down on a transparency.

Well, we can go over to much more important realm in
elementary particle physics, or in fundamental physics, I
should say.
And that is the work of Einstein.
Now we all know what kind of techniques he used
for getting his ideas.
They're described in numerous cartoons.
This is one of them.

When he proposed special relativity in 1905, he had to
get rid of the requirement of absolute space and time.

Ever since Newton's day, everybody knew that there was
absolute space and absolute time.
And here, Einstein was dealing with space and time which
transformed into each other to some extent, depending on the
state of motion of an observer.
If you run rapidly past the system, what was previously x,
becomes x and little bit of--
becomes mostly x and little bit of t.
And t turns into mostly t and a little bit of x, where t is
time, and x is distance.
So he was dealing with relative space and time, not
absolute space and time.
But everybody knew that there was absolute space and time.
He said, well, everybody may know it, but we don't need it.
Throw it away.
And he was quite right.

Another modest example from my own experience, proposing
quarks as fundamental constituents of
neutrons and protons.
People are always asking me why I chose that name, but if
you think about the sound, it's an obvious name for
fundamental constituent of atomic nuclei.

That wasn't the problem.

The problem was that I was violating several rules,
things that everybody knew.
Everybody knew that you don't have objects that a
permanently stuck inside observable objects and can
never come out to be detected singly.
But quarks are like that.
They're permanently stuck inside particles like the
neutron and proton, which they compose, and they can't get
out singly.
That's why there isn't another route 125 around Boston--
I mean 128 around Boston--
with quarkonics industries.
If the quarks could escape singly, they would have all
sorts of practical uses in industry.
But they can't.
They're stuck inside.
However the idea of particles being permanently stuck inside
was not a familiar one.
And most physicists thought it was impossible.
Just the very fact that the neutrons and protons are
composite, and made up of simpler things, was also not
orthodox belief.
They were supposed to be elementary.
Everybody knew they were elementary.
Third, the electric charges of particles were supposed to be
integral multiples of the proton charge,
so 0, 1 minus 1.
The quarks, however, have plus 2/3 and minus 1/3.
Well that's obviously wrong, because everybody knows you
don't have fractional charges.
However, despite all these prohibitions, despite
violating all these prohibitions, it turned out
that the idea of quarks was quite correct, and was
verified not very far from here at SLAC, on Sand Hill
Road, where my friends, Dick Taylor, Henry Kendall, and
Jerry Friedman took what amounts to an electron
microscope picture of the proton.
And they were able to deduce from that that it was actually
made, mostly, of three quarks.

Now we mustn't get the idea that any challenge to
scientific orthodoxy is likely to be right.
Quite the opposite is true.
Most challenges to scientific orthodoxy are wrong and very
many of them are crank.

What has to be verified, if challenging some accepted
idea, that it really can be dropped.
I've talked in these last few minutes about certain ideas
that could be dropped, but not every one can be.

You should always ask, why not?
But realize that usually there's a damn
good reason why not.

A few years ago, I was asked by a huge company to appear in
their television ad on the theme why not.
I didn't have to say anything good about the company.
I just had to say something about asking, why not?

I appeared for just a moment, but they paid me a reasonable
fee for it.
And next year, they were very pleased-- the following year,
they were very pleased with the reception of the ad.
And they ran it again, which means, according to the rules
of actors equity, that I got the fee again, and a second
year's membership in the Screen Actors Guild.

Then, they invited me to come to their headquarters and
speak to the management and also, through their intranet,
to all their employees around the world, at least in
suitable time zones, all on the same
subject, asking, why not?
And I emphasized that it's a very productive idea, to keep
asking why not, but that in science, there's usually a
very good reason why not.
I said I don't know much about business, but I assume it's
similar in business, that you should always ask yourself why
not about all sorts of ideas, all sorts of proposed changes.
But realize that there is generally a very
good reason why not.
You have to watch out always for certain things, I said.
One of them is profit and loss.
Even if though I'm not a businessman, I assume the
profit and loss are important, also, legal and ethical
considerations.
Well, they should have taken notes.

It was, of course, Enron.

Fortunately the fees were not paid in stock.

Now I mentioned that there were artists at
that meeting in Aspen.
What about art?
Well, for the visual arts, we can pay attention to the late
Kirk Varnedoe, a splendid guy who was the longtime head of
painting and sculpture at the Museum of
Modern Art in New York.
He wrote a book, which I recommend, called A Fine
Disregard: What Makes Modern Art Modern?.

And his idea is that in modern art, and also contemporary
art, which is still more recent, the artist plays with
the rules, instead of always playing by the rules.

The title of his book, A Fine Disregard, comes from the
inscription on a stone next to a playing field at Rugby
School in England.
Kirk Varnedoe was a former rugby player.
And he was very interested in that commemorative stone at
Rugby School.
Here's what was written on it, what is still written on it,
"this stone commemorates the exploit of William Webb Ellis,
who, with a fine disregard for the rules of football as it
played in his time, first took the ball in his arms and ran
with it, thus originating the distinctive feature of the
rugby game.
AD 1823."
So what we're talking about, in this connection, is problem
formulation, rather than problem solution.
And I believe that problem formulation is usually much
more important than problem solving, and in many cases
more difficult.
It doesn't look more difficult, but it turns out to
be harder in some ways, in many cases.
You have to ask, what are the real
requirements in this situation?
What are the real conditions that the
solution must satisfy?
If you get that right, then you can try and figure out
what the solution is.
There's one place, however, where the problems are
formulated for you, school.
It's almost the only place where the problems are
formulated for you.
And then you just solve them.
In almost any other place, in almost any other human
activity, the challenge is to formulate the problem and
then, later, solve it.
There is a very familiar exercise that all of you have
seen that can be made to illustrate this point.

Here's the diagram.
You've all seen it, nine dots, forming a square.
And you're asked to connect all the dots by drawing the
smallest possible number of straight lines without taking
the pencil off the paper.
And anybody can do it with five straight
lines, it's very easy.
To do it with four straight lines, which is possible, you
have to do something like this.
And you notice that the lines are outside of
the square at times.
That may be, for all I know, where the expression thinking
outside the box comes from.
This would be the box.
And these lines, which connect the dots, if you're going to
do it with four lines only, get outside the box.

At the Santa Fe Institute, where I work, we have a
resident cat.
And there's a cartoon posted on the wall that has a man
talking to his cat.
The cat is on the floor next to a tray of kitty litter.
And the man is shaking his finger at the cat and saying,
never, never think outside the box.

Now if we're going to solve this problem, you can solve it
in a trivial way, as we saw, by going outside the box.
But you can imagine other things besides asking, are you
allowed to draw lines that go outside the square?
But you can also ask, do you have to
treat the dots as points?
In the actual picture, they're little round dots.
They're not points.
They have widths.
Can you take the widths into account?
Are you allowed to?
Are you allowed to use the thickness of the lines, as
opposed to mathematical lines, which have no thickness?

Are you allowed to crumple up the paper and
drive the pencil through?
We can do it in one line.

Which of these is allowed?
Which of these are allowed?

This exercise and these questions about what's allowed
were treated in a somewhat different way from the way I'm
treating them, but this same general idea.
They're treated in a book by Professor Jamew L. Adams,
called Conceptual Blockbusting: A Guide to
Better Ideas.

They are also emphasized in talks by my friend Paul
MacCready, who developed the bicycle powered aircraft, and
the solar powered aircraft, and the flying, flapping
pterodactyl, and lots of other things.

Here's a letter that a 10 year old girl wrote to Professor
Adams. I'll read it to you, but it's also here so you can
look at it.
"Dear Professor James L Adams, My dad and I were doing
puzzles from Conceptual Blockbusting.
We were working mostly on the dot ones." And then she has
the nine dots here.
"My dad said a man found a way to do it with one line.
I tried and did it, not with folding.
I used a fat line.

It doesn't say you can't use a fat line, like this.

Actually, you need a very fat writing apparatus.

Sincerely, Becky Beagle.
Age 10." I wonder what happened to Becky Beagle.

Another thing we can say about creative ideas with
illustrations from physics, but also illustrations from
lots of other things, is that often a creative idea involves
taking an existing idea and building on it, taking it more
seriously than its original proponent did, and using it
for some other purpose.
We can look again at 1905, that miraculous year for
Albert Einstein, when, working as a patent clerk in Bern, the
capital of Switzerland, he had three ideas that he published
in the same volume of the German physics journal,
Annalen der Physik--

not only the same year, but the same
volume of the journal.

Special relativity is one, and we mentioned it.
But we didn't mention this interpretation of it.
One way to describe special relativity is to say that the
symmetries, the transformations of special
relativity are the symmetries of Maxwell's equations for the
electromagnetic field.
And what Einstein did was to take those symmetries, the
symmetries of Maxwell's equations, and apply them also
to particle dynamics, to the particles moving in the
electric and magnetic fields of Maxwell, so that the whole
problem obeyed the symmetries.
And the symmetries are the symmetries of special
relativity.
They are just the spacetime transformations of special
relativity.
Now those transformations were known already, especially to
the Dutch physicist H. A. Lorentz.
Lorentz found these transformations, exactly the
same ones that Einstein used later for special relativity,
and to this day they are called the Lorentz
transformations.
Why isn't special relativity attributed to Lorentz?
Well two things--
we've seen already that Einstein threw away absolute
space and time, and left only the relative space and time of
relativity.
Lorentz didn't do that.
He kept looking for a way to fit absolute space and time in
with the relative space and time.
And of course, he never found it.
Einstein simply took the step of cutting the Gordian Knot,
throwing away absolute space and time.
But there's another reason--
Lorentz didn't take the additional step of applying
these same symmetries to particle dynamics.
They remained just the symmetries is of Maxwell's
equations for electromagnetism.

It took Einstein to add the additional idea that these
transformations were general and they applied to the
particle dynamics as well as to the electromagnetic fields.

So Lorentz was a great man and did very important work here,
but he failed to see these two these two important points.
And so Einstein was taking Lorentz's idea more seriously
than Lorentz himself had.
That's even more obvious and even more striking in the case
of Einstein's work on the photoelectric effect.
In the photoelectric effect, a bit of light hits a metal
surface and knocks out an electron.
And Max Planck, in 1900, suggested the quantum, that,
for this purpose, electromagnetic energy came in
packets of energy, where the energy was Planck's constant,
h, times the frequency of the light, or of the
electromagnetic wave.
Well this was a rather revolutionary idea, but Planck
didn't carry it far enough.

He had the idea of the quantum all right, but not in
connection with the photoelectric effect.
It didn't occur to him that electromagnetism, in hitting
the electron and knocking it out, would come in
the form of a quantum.
If you do assume the quantum, in that case, you get this
simple equation of conservation of energy--
h Nv. Nv is the frequency.
h is Planck's constant.
This is the energy of the quantum.
The energy of the quantum equals the electron's kinetic
energy, plus the energy necessary to knock it out of
the metal, very, very simple equation.
But this equation worked.
It explained the data.
The data conformed exactly to this equation.
Planck didn't like it.
He had invented the quantum for other reasons.
He believed in the quantum for these other purposes.
But taking it more seriously than he had originally done
was not something he believed.
He didn't think that Einstein understood what he was doing
in applying the quantum to the photoelectric effect.
Nevertheless, Planck look favorably on young Einstein.
He recommended him for membership in the Prussian
Academy of Sciences, which is a rather high honor, and
eventually for the Swedish Medal, the Nobel Prize, which
Einstein didn't win for another 16 years.
And he got it for the photoelectric effect.
Finally people stopped objecting.
Even Planck, I guess, stopped objecting to his use of the
quantum in this connection.

Earlier, earlier on, Planck said, well, Einstein
is really very good.
He's a very good physicist. We'll forgive him this
youthful indiscretion of believing that the quantum can
be used here in the photoelectric effect.
But finally, in 1921, he won the Nobel Prize for it, just
for this equation.

A third thing that Einstein did in 1905 was to study the
Brownian motion.
You know what that is.
It was discovered by the English botanist, Brown,
around 1830 or so.
You can see it yourself if you look at something like ink in
water under a microscope.
You see the little particles of ink moving, randomly, in
little jerks.
And Einstein, and also the Polish theorist, Smoluchowski,
the same time, suggested that they were
being hit by molecules.
And Einstein worked it all out mathematically, and figured
out how many molecules per unit volume you would get in a
gas, and compared it with other estimates of that and
measurements.
And it all seemed to work.
And Smoluchowski did something similar.
What they were doing was taking seriously the notion of
a molecule.
Everybody agreed that molecules were useful in
chemistry, a sort of chemical bookkeeping.
But that the molecule was something that could hit you,
that could hit an ink particle and make it move, that was not
believed by most physicists.

But this work made it clear that the molecule was a real
thing that should be taken more seriously than it had
been taken by people who suggested it earlier.

Now let me close by discussing very briefly the notion of
teaching creative thinking.
There's nothing to tell us, a priori, that it's impossible
to improve creative thinking by teaching.
It might work.
It might not.
The proof would have to be in the pudding.

One man who has ideas about that and tries to teach
creative thinking does so very widely in many large
corporations and so on is Edward de Bono.

And his kind of reasoning can be represented this way.
He doesn't say exactly this, but this is something that
relates to the way he looks at things.
You imagine that you have a landscape of ideas, looking
like this, with shallow holes and deep holes.
And the deep hole is a great idea that you should get
eventually.
The shallow holes are less good ideas that will not solve
your problems. And the objective should be to get
somehow to the bottom of this deep hole and stay there.
Now if you're just moving downhill, if you're only
instruction is to keep moving downhill, because you think a
better idea lies in a certain direction, then you're likely
get stuck in a shallow hole, because there's lots more
shallow holes than deep ones.

However, if you have noise, or heat, or simulated annealing,
as is often called, so that there's a random motion
superposed on going downhill, then, if it's the right amount
of heat or randomness, you could be knocked out of all
the shallow hole, but not be knocked out of the deep one,
because of the tuning, the amount of heat, or noise, or
whatever it is you're adding to the system, so that it's
enough to knock you out of shallow holes, but not enough
to knock you out of a deep one.
Then, looking for the right idea would involve a tendency
to move downwards, modulated by some noise that knocks you
out of shallow holes, but still allows you to explore
the deep one.

So that suggests, if there's anything to it, it suggests
that you should apply that if you're trying to solve
problems. You should try to use something random, in
addition to all the logical, rational, reasonable inputs to
your thinking.
You should use something random.
So what Edwards suggests is looking at the last noun on
the front page of today's newspaper, and using that to
solve your problem.

That contributes enough noise that maybe you'll be thrown
out of the shallow holes, but perhaps you'll be able to
reach a deep one and stay there.
We shouldn't think that finding creative ideas is
restricted to these stratospheric realms of
science, and art, and so on.
It can also appear at any moment in every day life.
We're all faced with little puzzles every day, and the
more we have all this equipment in our lives, the
more it's true.

At any moment, we can be faced with something that requires a
creative thought.

One writer on this subject discusses the case of a
company picnic involving a lot of cheese.
No one, however, is thought to bring a
knife to cut the cheese.

But a young lady pulls out her credit card
and cuts the cheese.
That's a much more modest achievement than many of the
things we've been talking about, like special relativity
and so on, but it does involve a creative idea.
And it involves using something beyond the domain
for which it was originally proposed.
Well I'm very happy to answer questions and I regard this
little talk just as an introduction to a question and
answer session.
Thank you.

AUDIENCE: Well thank you for joining us.
I guess I have a couple things to say.
One of them is that--
I'm not sure how familiar you are with computer science, but
it isn't obvious to me whether it's yet a science, except
when it comes to debugging.
And I'm sure that when we're debugging,
we are doing science.
And people talk about the creative process in science as
coming up with models or explanations, but, at least in
my observation, there's two other steps that are highly
creative in the scientific method.
And one of them is coming up with a specific hypothesis to
test. And the third is coming up with a test for it.
MURRAY GELL-MANN: Yes, well I included those, as well.
I said that in science, you may be accounting for some new
data, or you may be proposing a new hypothesis, or you may
be suggesting a way, a prediction, making a
prediction that would allow a hypothesis to be tested.
I agree with you completely.
I actually said it.
You're completely right.
That's theoretical science.
There is also experimental science.
And there is also the making of equipment.
And all of those involve lots of creative thinking.
It's just that I was talking about theoretical science.
AUDIENCE: Yeah, not complaining.
I just wanted to sort of emphasize these areas that I
think are under-emphasized in discussions.
MURRAY GELL-MANN: Yes, you're quite right.
AUDIENCE: Thanks very much for the talk.
I'm an avid observer, amateur observer, of particle physics
and particle physicists, without being very
mathematical.
And I wondered if you had any thoughts on string theory and
string theorists, who seem to have lots of ideas, but very
little experimental evidence so far.
MURRAY GELL-MANN: Well, let's see.
I'm asked that question often.

I am an important patron of superstring theory.
When superstring theory was first developed in 1971, '72,
I thought that it would be very important.
I didn't know for what.
And I asked the people who were doing it to come to
Caltech to join my group, especially John Schwarz and
Pierre Ramond.
Andre Neveu, who wrote the original paper with John
Schwarz, came for a while, but then he returned to France.
But the other two stayed.
And we gradually build up quite a group at Caltech, part
of my theoretical particle physics group.
So most of the work-- a great deal of the work, anyway, that
was done on superstring theory between '72 and '84 was done
in my shop, not by me, but people who came there.
And during that time, we realized what the use was,
what the possible use was of superstring theory.
It was originally intended to be a theory just of the strong
interaction, the hadrons, so-called, strongly
interacting particles.
But it was discovered that it couldn't be a theory of the
strongly interacting particles, because it had a
particle with zero mass and spin two, which you couldn't
possibly have in a theory of the strong interactions.
There is no meson like that.
But there is a particle like that, the graviton, quanta's
gravitation.
So what this was was a candidate for a theory of all
the interactions, including gravitation.
And it was noticed in the middle 70s that a theory based
on superstrings would predict Einstein's general
relativistic theory of gravitation.
And it would predict it within quantum mechanics.
And without the crazy, infinite corrections, which
appeared in other attempts to unify general relativity and
quantum mechanics.
That's is what, in my opinion, made it very attractive.

It had a graviton, of course, which made it unsuitable to be
a theory of a strong interaction, but very suitable
to lead, perhaps, to a unified theory of all the forces and
all the elementary particles.
Well since then--
it's 30 years or so--
people have been trying to build a correct, unified
theory, or a good candidate for unified theory based on
super strings.
And they made an enormous amount of
progress in various spurts.
They haven't got there yet, however.
And some of the efforts look discouraging.
Some of the results of some of the efforts look discouraging,
but, in other cases, not so discouraging.
As to predictions, there will certainly be predictions.
We've already seen a retrodiction of very great
importance, namely the retrodiction of Einstein's
general relativistic theory of gravitation.
It is not negligible.
There's also the prediction that you have supersymmetry,
presumably broken supersymmetry, since we don't
observe exact supersymmetry.
Supersymmetry is a symmetry between fermions and bosons,
between particles that obey the exclusion principle, like
the electron, and particles that obey an anti-exclusion
principle, like the photons.
That anti-exclusion principle is what makes the laser
possible, of course.
Photons love to be in the same state at the same time.
And that's how you can have a laser beam.

The supersymmetry has to be broken to be compatible with
observation.
And it has to supply, for every elementary particle, a
companion with the opposite statistics.
In other words, for every fact elementary fermion, there has
to be a boson.
And for every elementary boson,
there has to be a fermion.
And these have received some peculiar names.
I was there when they were named, but I
did name them myself--
the selectron, for the electron, the photino company
is the photon, and so on and so on.
Now these things are being sought at accelerators.
When the new, bigger accelerator comes online near
Geneva next year or the year after, they will really step
up the search for these partners, superpartners of the
known particles.
And if some of them are found, that will certainly be
encouraging for theories based on superstrings.
Supersymmetry, broken supersymmetry is also very
good for an answering a number of other theoretical problems
that we have. But you could, of course, technically have
broken supersymmetry without having to superstrings.
So enemies of superstrings, who seemed to have turned up
in various places, can always say that.
But I think that finding superpartners will be very
encouraging for the possibility that one can
construct a suitable superstring theory, based on
superstrings.
But attacking a theory that hasn't yet been constructed is
a little strange.
I think mostly it's about money.
Some people would like some of the money that goes to the
smart people who work on superstring
theory to go to them.
Maybe they're right.
I don't know.

AUDIENCE: Thank you again for coming.
I have a more general question, which is the theme
of creativity.
You've described--
MURRAY GELL-MANN: I didn't talk about creativity.
I talked about creative thinking.
AUDIENCE: Creative thinking.
Well I--
I won't drag you into the difference.
MURRAY GELL-MANN: I think of it as something else.
It's some sort of probably inborn characteristic that
allows you to engage in creative thinking, and
creative projects in science and art, and so forth.
AUDIENCE: OK.
So I'll restrict myself to creative thinking, then.

The examples you've given of creative thinking are, I'll
say, directed--
once you have found the problem, there is a chunk of
cheese that needs to be cut, or there's an unexplained spin
that needs to be explained, and so you already have the
problem there.
And I'm just wondering if you have--
and there is a question of how do you think outside the box,
for example, to attack that existing problem.
But as you pointed out, there is this issue of--

as engineers we often have the problem in front of us.
There's something that's not running, or there is something
that is not running well enough.
But there's also this--
we find ourselves in the situation of looking for a
problem to solve.
OK, everything's cleared from my desk.
I'm an engineer, I'm a scientist, I'm an artist. How
do I decide--
can we apply creative thinking to figuring out, since we're
not in school, the problems aren't necessarily given to
us, can we apply that same, or some similar heuristics to
figure out what problem we should be attacking next.
MURRAY GELL-MANN: Well, that was the
subject of my talk, really.
I said that problem formulation is usually much
more important, and in some sense--
not an obvious sense-- but in some sense, more difficult
than problem solution.
You have to find out what's wrong.
Where is it itching, so I can scratch it?

And that's tricky sometimes.
What rules do I have to obey in order to get something, in
order for me to be allowed to have something new?
What rules do I have to violate, what rules can I
violate, without running into a contradiction, or running
into a contradiction with nature, and
so on and so forth.
So it's precisely as you say, that the most important time
is when you are not sure what the problem is.
You have a piece of equipment that isn't working, maybe
shouldn't have that kind of equipment.
AUDIENCE: But when the equipment is working--
MURRAY GELL-MANN: Maybe you should have a different kind
of equipment.
You're generating energy in some particular way.
Maybe you should generate it in some other way.
Or maybe you shouldn't generate it at all, but save
energy, and so on and so forth.
AUDIENCE: But when the equipment isn't working,
that's sort of a problem.
It may suggest an open issue that's completely unrelated to
the equipment not working, but essentially that's where
something is itching.
I guess what I'm finding is--
MURRAY GELL-MANN: Not necessarily, not necessarily.
And even debugging, which was mentioned, is
an interesting topic.
We all know of a gigantic corporation
that does no debugging.
It allows the customers to do that.

That was an interesting invention.
Imagine being able to make money by selling a whole lot
of products that don't work and letting your customers
figure out how to improve them.
It's a great idea.

AUDIENCE: I wanted to ask you about another creative idea
that's about 30 years old, and that can potentially change
the way we work here.
What is your take on the future of quantum computing?
MURRAY GELL-MANN: Quantum computing.
Well, so far, one hasn't gotten it terribly far with
it, except for a lot of ideas.
And the ideas are two kinds, of course.
One is how we might be able to make a quantum
computer that works.
And the second is what kinds of problems could
it solve for us?

What sorts of things would be changed by
having quantum computers?
Well, originally, people thought that it would be very,
very, very difficult to maintain the coherence for
long enough, for over a big enough range, to have a
functioning quantum computer, but that once you got it, it
would be able to solve all sorts of problems in
polynomial time, which is thought to require
exponential, or worse, time to solve.
Well it hasn't quite turned out that way.
Mr. Shor, of course, found that one famous algorithm
involving factoring huge numbers into their prime
factors, that that could probably be reduced to a
problem soluble in polynomial time.

But other than that, there hasn't been any proof of that.

Instead, people have stopped thinking that it's necessarily
so difficult to maintain the coherence, because they have
all these error correcting algorithms that might succeed
in canceling out the inherent noise in the quantum computer,
and allow for a situation that would resemble a situation
with a lot of coherence.
So it's just turned around, as far as I can tell.
The ideas about quantum computers have turned around.
It's maybe not so difficult to simulate the coherence that
you need through all these error correcting procedures.
But it may be difficult to find a problem that the
quantum computer will solve better.
And people started thinking, therefore,
about quantum system.
What about simulating quantum system?
Quantum computer might be really good for that.
And it's quite different from the kind of use that people
had in mind some years ago.

But so far, the quantum computers have very, very
limited capacity.
And as my good friend Seth Lloyd says, a two bit computer
is a two bit computer.

We've wondered where our alumni of the Santa Fe
Institute would get jobs.
And we worried whether they would get jobs at all, because
they're all highly interdisciplinary.
But academic jobs seem to be available, provided you don't
try to predict in what department.
Some of our physics trained people
have ended up in sociology.
One professor at Columbia, who spent a long time at the Santa
Fe Institute, a very brilliant guy from Australia, said that
the first sociology class he was ever in was the one he was
teaching as a full professor.

So Seth Lloyd has become a professor of mechanical
engineering.
And because he's trying to develop quantum computers, he
says he's a professor of quantum mechanical
engineering.
It satisfies everybody.
But he is the one that says that the two bit computer is a
two bit computer.
That's all we have so far.
I don't think I've answered your question, but--
[INTERPOSING VOICES].
AUDIENCE: No, it's okay.
My question actually ties into that.
One focus of creativity would seem to be interdisciplinary
in applying things you've learned, or approaches from
one field, to a very different field.
And again, speaking as an amateur in physics, it seems
like the two things that at least get the most publicity
outside the field right now are superstring theory and the
whole dark matter, dark energy issue.
I never hear anything about how those combine.
Is there any sort of combination of those?
MURRAY GELL-MANN: Well, let's say what dark matter and dark
energy are.
They're not very good names.
Especially dark energy is a really dumb name, especially
because people could mix it up with dark matter, with which
it has almost nothing to do.
Dark matter refers to the fact that galaxies and clusters of
galaxies are made up mostly of different material from what
we're accustomed to discussing, not stars and
planets, ordinary molecules, and so on and so forth, made
of something else.
That's called dark matter.
And the superpartners of known particles may well make a
major contribution to so-called dark matter.

I used to walk by the astronomers table at the
faculty club at Caltech while I was still teaching there.
And I would say to them, don't you guys realize you're
talking just about 4% of the universe?
Everything else is photinos.

They didn't like that.

However, it was perfectly true.
We don't know if it's photinos, but it's something.
There may be several kinds of dark matter.
Now dark energy is a really dumb name for the discovery
that the recession of galactic clusters, that's called the
expansion of the universe, is accelerating.
The expansion of the universe, you have to realize, if you're
a lay person in this business, doesn't mean that atoms
receded from one another, or that rocks recede from one
another, or planets and stars recede from one another.
Not even galaxies recede from one another.
It's clusters of galaxies, gravitationally closed, that
undergo a recession from one another.
And with the discovery that this recession is accelerated,
we're back to the old question of the cosmological term in
Einstein's general relativistic equation for
gravitation.
He introduced this cosmological term because he
wanted a static universe.
He didn't realize that there was observational evidence for
an expanding universe.
He wanted a static universe, and since the universe would
collapse under gravitation, which is purely attractive, he
had to introduce something else that would stabilize it.
So he introduced this extra cosmological constant, a
single constant, added to the equation for gravitation.
And then he realized, through the work of Hubble in
Pasadena, that the clusters of galaxies were receding from
one another and you had an expanding universe.
So he then said, oh, this is a terrible mistake.
I've committed this terrible error of introducing this
extra term marring the beauty of my equation.
And it's not necessary, because we have an expanding
universe, and it will either keep on expanding, or
eventually contract, and we don't have to worry about this
extra term.

But now it's back, apparently, or something like it, either
that or something very like it, in order to explain the
acceleration of the expansion of the universe.
The question is, why does it have the value that it has?
The funny thing isn't that it's non-zero.
If you look at it in the light of particle physics, there has
to be such a term.
It's the average energy the vacuum or something.
It's a fairly obvious thing, and it must be there.
The question is, why is it so tiny?
Because if you try to estimate from particle physics what
kind of a value you might have for it, the discrepancy
between that and what is seen, assuming that what is seen
really is a cosmological term, the discrepancy is by a factor
of 10 to the 118th, which is the largest fudge factor in
the history of physical science.

And that's a really good question.
I would like to know the answer to that.

AUDIENCE: Thank you so much for coming, Dr. Gell-Mann.
I'm curious, having spent a lot of your career in
something called theoretical physics, what are the
applications of your work that have given
you the biggest thrill?
MURRAY GELL-MANN: Applications?
AUDIENCE: Yeah, for instance the laser, microwave oven.
I mean, are there things, are there pieces of technology
that we have in the real world that you, knowing the physics
behind them, you look at that and say, wow, that's really
need, and I helped contribute to that.
MURRAY GELL-MANN: I can't think of any applications.
But it takes a while, you know.
I mean, I'm very, very, very old now.

If you want to think of me as a child prodigy, I'm a very
old child prodigy.
Anyway, nevertheless, not old enough to see the applications
of the things I worked on.
Take the laser, for example.
It came out of Bose Einstein statistics, as I said, the
fact that photons like to be in the same
state at the same time.
And this was proposed theoretically in 1917 and
1920, by Einstein and by the Indian, the Bengali physicist,
Bose, or Bose.

But it wasn't until 40 years later that we got the laser.
And the same kind of time interval may apply to lots of
other fundamental ideas and fundamental discoveries, that
they don't lead to gadgets until much, much, much later.

Now if the quark had been able to escape singly from it's
prison, we would have quarkonics, for sure, lots and
lots of applications, including mediating
thermonuclear fusion.
But, sorry.

AUDIENCE: I'm curious.
I've noticed that the experimental physics is
getting increasingly expensive, for example at the
LHC, where they're building something very large which may
or may not discover a stop particle.
MURRAY GELL-MANN: May not discover what?
AUDIENCE: The stop, super top.
MURRAY GELL-MANN: Oh, I see, yes.
AUDIENCE: I'm curious what you think about computational
approaches like lattice gauge theory or--
MURRAY GELL-MANN: Oh, that's very good, of course, but it
doesn't substitute completely for experiments.
No, at Santa Fe Institute, we do a lot of simulation, and
modeling, and so on, with computers.
And computer experiments are extremely important.
But they extremely important usually when you have some
model or theory of what's going on and you want to
understand it's consequences.

But we also need to know what's actually
happening out there.

We waste a lot more money on a lot of other things.
I wouldn't worry about wasting money on particle
accelerators.
If there is another one, it will be for the whole world, a
single one for the whole world, an electron-positron
collider, like SLAC, here at Stanford, but
much, much, much bigger.
That would be a world machine, with contributions from all
the countries involved.
And that's still for a number of years ahead.
AUDIENCE: So one anecdotal, I wish we could get the US
patent office to have the--
I wish we could get the US patent office to have the
hiring standards of the Swiss patent office.
But in 2000, Michael Crichton, an author, observed that there
were a number of anomalies in physics that were, in theory,
going to be explained by simple changes to the standard
model and whatnot.
And he likened it to the period of physics between the
1890s and early 1900s, where quantum mechanics and all
these changes occurred in the way we thought about things.
I was wondering--
MURRAY GELL-MANN: No, they didn't occur, is what you are
trying to say.
There were all these contradictions of classical
theory that people didn't take the step of dropping a whole
lot of ideas and substituting entirely new ones.
They did that a couple of decades later.
AUDIENCE: Right, so I was wondering what anomalies--
I mean, i read in the late press--
MURRAY GELL-MANN: I don't know.
I don't get my scientific education from this very tall,
medical student.

AUDIENCE: What questions do you think will be important to
be answered in this couple of decades?
MURRAY GELL-MANN: What questions will be--
AUDIENCE: What questions in physics.
MURRAY GELL-MANN: Well, I just listed some.
Do we really have superparticles, so we have
approximate supersymmetry, and super Yang-Mills theory, super
gauge theories?
Do we actually verify all that?
Do we get to understand the size of the cosmological
constant, or whatever replaces it, in explaining the
acceleration of the expansion of the universe?
And what about constructing a unified theory based on
superstring ideas?
Will that be successful?
Will we verify the existence of an actual Higgs particle,
one or more Higgs particles, rather than finding some kind
of Higgs-like mechanism that doesn't involve a new
particle, in order to explain the masses of otherwise
massless particles, and so on and so forth, lots of very
well known questions.
I don't know what this guy has in mind.

AUDIENCE: Well someone has to ask this question.
Dr. Robert Boussard was here a few months ago.
MURRAY GELL-MANN: Who was?
AUDIENCE: Robert Boussard.
MURRAY GELL-MANN: Oh, really?
The twin person?
The twin guy?
The guy with the twins studies, identical twins
separated at birth?
AUDIENCE: He may have done that as well, but he was here
for another reason.
MURRAY GELL-MANN: No, no, this is a different person.
OK, who is it?
I don't know who it is.
AUDIENCE: He was talking about an extension of the Farnsworth
containment mechanism for fusion.
MURRAY GELL-MANN: The what?
AUDIENCE: For fusion.
MURRAY GELL-MANN: I'm sorry, I just don't understand.
I don't know what you're talking about.
You're talking about some field with
which I'm not familiar.
AUDIENCE: Electrostatic containment of fusion.
MURRAY GELL-MANN: Pardon?
AUDIENCE: Electrostatic containment of fusion.
MURRAY GELL-MANN: Oh, containment of plasma?
Containing milk in rubber bands?

It's hard.
AUDIENCE: Well, I was going to ask you if you evaluated his--
[LAUGHTER]
MURRAY GELL-MANN: I'm sorry.
I didn't hear.
AUDIENCE: I was going to ask you if you had
evaluated his work.
MURRAY GELL-MANN: I don't know any of this.
I'm sorry.
I did follow some developments in the attempts to achieve
practical thermonuclear fusion, some years ago.
It's been going on for a long time.
It's 56 years, I think, the US that has been working on this,
and probably a bit longer elsewhere.
It was a highly classified to begin with,
in 1951 or so, '52.
While it was very highly classified, they had a meeting
at Berkeley of people working on various approaches to
thermonuclear fusion.
And it was held in a movie theater.
And the project was called project Sherwood.

People brought pads of paper into the meeting to take
notes, but then they had to turn the pads of paper over
the security guards as they left, even if they were blank.
However the owner the theater was a wag, and a wag with
access to some knowledge, because the marquee of the
theater had two movies listed, which weren't playing at all.
But the titles were up there.
Men of Sherwood and Top Secret.

That's all I know.
I'm sorry--
AUDIENCE: Thank you very much, Dr. Gell-Mann, for your
contributions, and for your talk here.
There's a fine line between being a creative innovator and
being a disruptive nuisance.
It can be argued that it is equally or more important to
communicate persuasively, as it is to think creatively.
What are your thoughts along these lines?
MURRAY GELL-MANN: Oh, I think it's always good to do that,
to persuade people.
But there are some people whom it's very
difficult to persuade.
And to waste one's energy on perpetual debate with those
people is probably not a good idea.
But there are other people who are accessible to reasonable
arguments and so on.
And once you deal very gently with them, and
try to persuade them.
Or maybe they're right and you're wrong, in which case,
you should let them persuade you.

AUDIENCE: I've read that you had interest
in a number of languages.
MURRAY GELL-MANN: I'm interested in relationships
among language.
[INTERPOSING VOICES].
MURRAY GELL-MANN: I have a project of that kind involving
some brilliant Russian linguists.
AUDIENCE: And you're fluent in 13 or so?
MURRAY GELL-MANN: No.
You know you can't trust things like that.
AUDIENCE: Is there any interaction between--
MURRAY GELL-MANN: I mean, I'm not recommending that you burn
all copies of this, but it doesn't contain only things
that are true.

AUDIENCE: Is there any truth at all to that
section of the page?
MURRAY GELL-MANN: Well, I don't speak languages other
than American English correctly.

But I know a little bit about languages, and I'm sort of an
honorary linguist, an honorary amateur linguist. And I'm very
interested in the relationships among languages.
And I've learned quite a bit, as a result.
Naturally, I know a few words of various
languages as a result.
But that I speak correctly some large number of languages
is just not true.
AUDIENCE: Is there any an interaction between creative
thinking and languages, or learning languages, that
you've come across in your study, in your amateur study?
Thank you.
MURRAY GELL-MANN: I don't know.
I'm not sure.
I'm not sure about that.

I haven't--
I'm not sure whether there is such a connection.

Well, I guess that's it.
Thank you.