[Music]
>>Steve: All right, three, two, one.
Our guest today is Sabine Hossenfelder.
She is a theoretical physicist, a longtime
friend of mine.
She is currently at the Frankfurt Institute
for Advanced Study, and she has a new book
out which we'll discuss.
She also has written recently an editorial
that appeared in The New York Times and actually
ruffled the feathers of a lot of high-energy
physicists.
We'll get into that as well.
I want to say at the outset that I anticipate
angry reactions from one individual and one
group of people from having you on our show.
The first, the individual, as you know, is
Luboš Motl, who will probably send me an
angry email asking me why I had you on my
show, and then the high-energy physics ATLAS
group at Michigan State will be angry because
they didn't like your New York Times editorial.
So having said all that, let's start by talking
a little bit about your biography.
I like to introduce our guests a little bit
by having them tell me just a little bit about
their life story.
One of the interesting things that you said
in your book was that you got into physics
because you felt you could not understand
people, and maybe you can just explain when
you realized that and, you know, if that was
when you were a child, how your childhood
might have been different from other people's.
>>Corey: And hopefully what you meant by not
understanding people.
>>Sabine: Yes, that's right.
So I wrote in my book I went into physics
because I don't understand people.
I've always felt that really, the natural
sciences and physics in particular are the
easiest part to understand about the world.
When it comes to human beings, you know, things
get complicated very, very quickly.
I have a lot of difficulties understanding
why people do what they do.
I thought that going into physics was kind
of the safe thing to do, you know: I would
be sitting there with my equations and try
to understand how the universe works, and
I wouldn't have to bother all that much thinking
about all this human baggage.
But it didn't quite work out that well.
It turns out that there's a lot of sociology
in science, somewhat more than I anticipated.
Yeah, people sometimes ask me how I got into
talking so much about sociology.
It's not that hard to understand.
So I originally studied mathematics, and I
had a boyfriend who also studied mathematics
but he also studied sociology, so naturally
I developed an interest in sociology, especially
for what the mathematical modeling is concerned.
And that was at the time in the mid '90s when
Stuart Kauffman's book At Home in the Universe
came out, and I got very interested in this
idea of agent-based modeling and complexity
systems and self-optimization and all that
kind of stuff.
And so it was kind of obvious to try to apply
the system's thinking to science and the people
in the system themselves — and once you
have the system thinking in your head, it's
really hard to get rid of.
>>Steve: I think you and I had a lot of discussions
just after the financial crisis about agent-based
modeling of economies and things like this.
But specifically to physics, I think I am
very sympathetic to your views on this: that
the type of person who goes into physics at
the beginning is a very rational person, or
thinks of himself or herself as very rational,
[laughs] and kind of looks forward to the
physics world as being kind of like the Vulcan
Science Academy, where everyone is completely
logical and rational; and then when you actually
get into it it's just another branch of academia,
where there's tons of sociology, it's maybe
less meritocratic than you had hoped, and
there are battling cliques trying to advance
their own interests and own theories.
Maybe you can comment on your sort of realization
that this was the case.
>>Sabine: Well, I guess it took me some while
to figure out.
I really only noticed this when I started
getting into the community of particle physicists.
So originally I come from a completely different
community, which is heavy ion physics, because
that's what people did at the institute where
I made my PhD.
But I never myself really worked on heavy
ion physics, so I was kind of shielded from
this whole community thing because it didn't
really concern me, like I just did my thing,
and we had a group that was like five people
and that was pretty much the contact that
I had.
And I didn't want to stay in Frankfort.
I moved to the United States after I made
my PhD — I was in Tucson and then in California
— so I started going to those particle physics
meetings.
I also mentioned this briefly in the book.
There's first and foremost the SUSY conference
about something like supersymmetry and the
fundamental interactions or something — so
it has this complicated name that I keep forgetting,
but everyone calls it the SUSY conference
— that used to be a really huge conference.
It since shrunk down a little bit, but it
used to be like 800 people, so one of the
really large events in the field.
I found it really creepy that when you were
listening to people, they were all literally
saying the same thing.
You would be listening to the plenary talks
and to the talks in the parallel sessions,
and they all had the exact same motivations
for why supersymmetry is the right thing to
do.
They were never talking about any shortcomings
of their models.
I'd ask them a question like about naturalness
or something like that, and they would all
give the same answers.
It just freaked me out, you know, I thought
that's not really how it's supposed to be,
there's something strange going on here.
You know, I looked into this issue with naturalness
(and I go on about this in the book) and that
was really kind of the deal-breaker, why I
didn't want to have actually to do with it
anymore.
And so I decided to get out of this community,
and then I started working on the phenomenology
of quantum gravity, where basically there's
no community [laughs] — maybe there's a
little community now, but it's like maybe
a hundred people or something, so not in the
order of thousands.
>>Corey: Can you tell us what's meant by naturalness
in the theoretical physics community? — because
it's a big part of your book.
>>Sabine: Yes, so naturalness is one of the
criteria for theory development that has become
very influential — in particular in high-energy
particle physics, but also in cosmology to
some extent — and it's a criterion that
you expect a good theory to fulfill, that
basically says that the parameters in that
theory — so that's the numbers without units
— they should be of order 1, so they should
not be really large, they should not be really
small.
And so that's the general notion of naturalness.
And then in high-energy particle physics they
say actually a more relaxed version of naturalness
that says well, sometimes very small or large
parameters can be okay if there is reason
for that, you know, if you have an explanation
— symmetry, for example, can be an explanation
for that.
That's this idea of naturalness.
And I call it an argument from beauty, because
I think that's where historically it comes
from; but some philosophers have told me I
should just call it a metaphysical argument,
or maybe just a philosophical argument, or
maybe it's just a belief.
So I don't really care what it's called.
The point is that it's an additional assumption
that you impose on your model.
>>Steve: Maybe to elaborate a little bit more
on that, I think it's fair to say that it's
not a completely well-defined notion of what
naturalness is.
It was a — I don't know about the current
situation, but certainly when I was a student
and early in my research career and well into
my research career — it was a dominant notion
that if you noticed some aspect of a model
of fundamental physics where there were some
strange coincidences — so, for example,
some number had to be extremely large or extremely
small to fit the data — and I'm talking
about a dimensionless number, so not something
measured in units, because obviously big or
small depends on what units are used to measure
it in — but in some models, many models
there are dimensionless numbers sort of given
by God, if you like, and why should this number
have to be 10 to the minus fifteen [10-15]
in order to fit the data?
The most well-known case is, the mass of the
Higgs boson is much lighter than if you just
sort of randomly put down numbers of order
1 into your model you would get a much heavier
Higgs boson, and so it was considered a huge
mystery why the Higgs boson would be so light
or its mass would be so small.
Now, as Sabine points out, it's fundamentally
a kind of aesthetic question.
So you can write down a mathematical model
that fits all the data, and then the question
is, are you happy with the model, or do you
find that because it has some "unnatural"
aspects that you suspect there's actually
a more fundamental theory underlying it that
you have yet to discover, which would explain
that unnaturalness.
>>Corey: So this seems to be an added constraint
that's a part of physics that I'm honestly
not sure if it's part of other fields.
I think almost everyone's familiar with Ockham's
razor and the idea that the theory should
be simple; and my question to you is, do you
see this as simply an extension of Ockham's
razor, or an added limitation that physicists
are placing on their theories, that be natural
in addition to being simple?
>>Sabine: So it's definitely not Ockham's
razor because, loosely speaking, if you think
of a theory in physics as some collection
of mathematical axioms together with some
identification of those mathematical things
with observables, then Ockham's razor is basically
a statement about the number of assumptions,
so it tells you that if there's anything superfluous,
get rid of it.
So that's basically Ockham's razor.
Naturalness instead is an assumption about
the type of axioms that you use.
One of the axioms that you will use, for example,
for the Standard Model might be something
like the mass of the Higgs boson is so and
so, and then you can ask well, is there a
better explanation?
And so the issue with naturalness is now that
people claim that for certain numbers you
need to have an additional explanation.
Let me maybe phrase this differently, because
sometimes people claim that I'm saying we
should not look for deeper explanations, which
is nonsense, of course.
So generally you would always want to have
a better explanation, say, for the values
of the masses in the Standard Model.
But the use of this criteria from naturalness
is that scientists say there are certain numbers
in those theories that particularly require
our attention and require an explanation — and
the mass of the Higgs boson is an example
for that, so it's supposed to guide your attention
basically.
What happens is that people focus on solving
this particular problem to develop new models,
and what I'm saying is basically, well, you
know, the mass of the Higgs boson is not in
anymore need of an explanation than all the
other masses in the Standard Model — they're
just parameters, they may just be whatever
they are and that's the end of the story.
So it's not a good problem to work on.
So that does not mean that it wouldn't be
nice to have an explanation for that — it
certainly would be — I just think that it's
not a promising route to make progress.
>>Steve: I think the sort of weak use of naturalness,
that I think maybe very few people would doubt
is reasonable, is just to say that, if you
see some aspect of your model that looks "unnatural,"
perhaps there is an underlying something that
you've yet to discover which explains that
unnaturalness.
But it doesn't have to be the case.
We don't know whether that is going to be
the case in the ultimate theory of everything.
>>Corey: In your book I really liked your
example from the Copernican theory and trying
to explain while the heliocentric model wasn't
accepted.
And you had an example of naturalness from,
you know, effectively five centuries ago that
I think for laypeople might allow them to
get a grasp of the idea, whereas most people
aren't gonna get Higgs boson.
Could you explain how you thought that the
naturalness argument played a role in people
trying to reject the Copernican theory?
>>Sabine: Yeah, so this was the first historical
example that I could find, and it went roughly
speaking like this: so if you have a system
where the earth is in the center and the planets
and also the sun go around the earth, then
it's natural to expect that the stars do not
move, because by assumption, kind of, the
earth is in the center and so why would they
move?
Now if you have a system where the sun is
in the center and the earth goes around the
sun, then you would expect the relative positions
of the stars to each other to change over
the course of the year, and this is called
the parallax.
At the time astronomers could not see it,
so what they concluded from this is that either
this parallax is very small, which would have
meant that the stars had to be very far away,
or we sit in the center of the solar system.
For some while at least, they thought that
this was a good argument for the earth being
in the center of the universe, and it was
based on this argument that there should not
be this large gap in the scales between the
distance between the known celestial objects,
with the planets at the time and the stars.
So now, of course, today we know that the
stars are actually much further away than
the planets in our solar system, and that
there's nothing unnatural about it because
that comes into being by a rather complicated
process where galaxies form and the solar
system forms, and so on and so forth.
Implicitly what went wrong there is that the
astronomers at the time assumed a certain
distribution of the objects that they thought
was natural.
Well, it did not work out.
So that's, I think, one of the first arguments
from naturalness, and to a certain extent
the arguments that are being used today are
still kind of similar, the idea that you don't
want this mismatch in the proportions.
It's just that they have become much more
abstract, and especially when it comes to
the mass of the Higgs boson, we're not actually
talking anymore about quantities that are
indeed observable.
You were speaking about a random distribution
of the parameters, from which you may conclude
that the mass of the Higgs boson is kind of
unlikely.
The thing is that you never actually observe
those parameters, by assumption.
The only thing that you eventually observe
is the mass of the Higgs boson, and that's
something which you measure either which way.
From what the content of this argument is
concerned, it's entirely philosophical, it
has no relevance for the computation of any
actual observable.
>>Steve: Well, I guess the way...
When I was a student and I first learned about
this issue with the Higgs boson mass, I always
said to other people, you're making a kind
of a priori assumption about the measure or
the distribution of parameters in the more
fundamental theory, which — and we don't
know what that distribution will be — subject
to your prior, maybe you strongly suspect
some special conspiracies going on to keep
the Higgs boson light.
But it is subject to that prior.
That brings me to the subject of aesthetics.
So there's a famous comment about the unreasonable
effectiveness of mathematics in describing
nature, and I think all scientists sort of
appreciate that to some degree; but that naturally
leads into what I sometimes refer to as the
tyranny of aesthetics.
So the notion that there will be simple mathematical
models that successfully — perhaps unreasonably
successfully — describes nature, naturally
leads your brain to sort of want to see beautiful
aesthetic models and to desire them.
And so the question is, you know, have we
gone too far in valuing aesthetics as a kind
of principle for model selection?
>>Sabine: Well, the problem is not aesthetics
per se, but that physicists are using very
narrow conceptions of beauty, like this criterion
from naturalness.
You could have the attitude to say, well,
if it describes nature then it's beautiful,
right?
But that's exactly not what physicists are
doing.
It's that they are postulating certain kinds
of symmetry that they want a more fundamental
theory to fulfill — for example naturalness,
but also they like to have more symmetries,
and they also like it to be simple in an absolute
way — so not in the sense of Ockham's razor,
that if you have several different theories
you take the one that achieves the most with
the least input, basically, but they want
a theory that is simple, period.
A good example for this is string theory.
String theory is based on a very simple idea:
everything's made of strings — and then
the devil's in the details.
But so I think the reason that a lot of theoretical
physicists like string theory is that it has
this all-encompassing, unified aspect that
comes from this very simple idea, and I think
that makes it appealing.
And I can certainly understand that appeal.
It's just that I don't see any good reason
why, if we look deeper into the structure
of matter — or if you want to include spacetime,
maybe one should say, deeper into the structure
of reality — why the laws necessarily must
continue to get simpler.
I see no particular reason for that.
>>Steve: Yes, I think that's a prior, that's
a prior that we hope will be realized.
Before we get into string theory, can we discuss
a little bit more particle physics?
Your editorial in The New York Times, could
you just recapitulate in a couple of sentences
what you were trying to get across in your
editorial?
>>Sabine: Yeah, so I was trying to get across
that, given the information that we currently
have, building a next larger particle collider
is not a good investment, if what you want
is to make progress in the foundations of
physics.
It's a very expensive experiment.
From the experimental foundations of physics
you can think of building the next larger
collider, and it is, I think for what's presently
on the tables, it's the most expensive one.
But we don't have any good predictions that
there should be anything new to find.
So of course you can say well, let's just
measure more precisely the properties of the
particles that we already know, and that's
all well and fine.
It's just that we run the risk that we build
this machine, and the only thing we get within
the next 30 years is more confirmation of
the Standard Model.
And now we do have problems in the foundations
of physics that we know require a solution
— dark matter is one of them, congravity
is also one of them — and so the only thing
we get is further non-results.
It will not help us developing this theory
further.
And so my argument is basically, there are
better things we could be doing with the money.
>>Steve: Right.
>>Sabine: And of course, particle physicists
don't like to hear that.
>>Steve: So we're talking about a sort of
50 to 100 billion dollar machine, and I would
say the only likely place it could be built
is in China.
And even a couple years ago there were some,
I guess, very optimistic people who thought
the Chinese government had sort of put something
into their five-year plan about possibly doing
this.
But just to be precise, I think your argument
is that, were that money to become available,
it would be, there are better uses for it
within physics than to build sort of the next
huge machine.
Is that fair?
>>Sabine: Yes, given all that we currently
know.
You know, I always make this little asterisk
and say that this is actually important information
to take into account.
So certainly, if — so the LHC is not done
right?
So they are now having their upgrade, then
there will be the third round, and then there
will be the upgrade to the high luminosities
phase.
And so if they find something new there, you
know, if maybe we're lucky and some supersymmetric
particles will show up after all, we'll totally
change this argument, of course.
>>Steve: Yes.
>>Sabine: But currently it doesn't look like
there is anything new.
Given all that we presently know, I think
it would be better if we collected more information
about aspects of our measurements where we
know we have something that needs explaining.
Like dark matter, for example: there's certainly
more things that we can measure that might
help us try to find out what it is, which
then again would help us to make better predictions
for what experiment to build here on earth
to maybe reproduce those things.
You know, if it's a heavy particle, then yes,
building a next larger particle collider would
be the thing to do.
But maybe it's not, you know, maybe it's a
really light particle, and you need a completely
different type of experiment.
It seems to me just smarter to first figure
out in more detail what is going on, and put
some more money into this.
And that's also for quantum gravity — I
already mentioned this — we at least know
that there has to be an explanation for this,
whereas when it comes to the Standard Model,
that just might be it, you know — all the
way up to the Planck scale, of course, you
know, but that's like a factor of a billion
or something away from what even the next
larger collider can test.
>>Corey: We periodically read about discoveries
coming out of the LHC, the Large Hadron Collider,
and I think most people have seen it — at
least people are informed — as an incredible
success.
We found the Higgs boson, it's a very exciting
discovery.
But your book is painting a very different
picture.
You're trying to say that in many ways it's
been a failure, we haven't found anything,
as I recall, predicted since 1973.
We've found these things that are predicted
before that, but none of the new theories,
predictions have been confirmed by the LHC,
and that's, as I understand it, part of what
makes you skeptical about putting more money
in a larger collider.
Could you maybe let me know am I right about
that, or react to that?
>>Sabine: So I don't think that the LHC has
been a failure, and I don't think I ever said
that, I'm pretty sure, because I think it's
been a huge success, because we knew that
there had to be some new physics to appear
at the Large Hadron Collider — not necessarily
the Higgs, but something had to appear.
And that was the case, so they found the Higgs
and everyone was happy, you know, the champagne
bottles were opened and all that kind of stuff.
What has been a failure have been the predictions
for new physics beyond that, and those are
predictions that physicists started making
soon after the completion of the Standard
Model, started with this idea that there had
to be a grand unified theory that then predicted
proton decay and experimentalists looked for
that — maybe they're still looking for it,
but they haven't found anything.
So some of those models were ruled out, but
you can always go and twist those models.
And then there has been supersymmetry, of
course, which was always supposed to be found
on the next larger collider, basically.
There are various dark matter candidates that
have been looked for in dozens of experiments
and not have been found.
So this is why I say, you look at what the
theorists have been doing: those predictions
have been wrong for 40 years.
The prediction of the Higgs actually predates
the completion of the Standard Model in the
'70s — it was made in the 1960s — so what
the LHC actually did was that it confirmed
the prediction that's even older than the
Standard Model.
>>Corey: But you do claim that there been
no new data in decades.
So what do you mean by that?
>>Sabine: There has been a lot of new data,
like the LHC collects a lot of new data every
time they make collisions.
It's just that this data only confirms the
theories that we already have.
What we do not have is data for some new physics,
some new phenomena, something that would help
us develop those theories that we're trying
to get done.
We have a lot of non-results from those dark
matter searches, for example, you know.
Every time they complete a search and find
nothing, you get better constraints.
It's just that if you want to find out what
the particle is, it's not particularly useful
information.
What you really want is, you want to have
an event where the damn thing actually interacts
with your detector.
And it's the same with these searches for
supersymmetry.
So you can say, well yes, so we've run the
LHC for 10 years now, and this has ruled out
a lot of the parameter space of supersymmetric
models.
But does this actually tell us what is going
on with quantum gravity or with dark matter
or what have you?
No, it doesn't.
So what have we learned from it?
>>Steve: If I could maybe clarify for our
listeners, so...
There were pre-existing models of fundamental
physics, say the Standard Model, which predicted
some particles which had not yet been directly
seen or discovered, and so LHC was a huge
success insofar as it discovered the Higgs
boson, but that had been predicted long ago.
If you look at new theories, new ideas written
down by theorists in the last, say, 30 years,
basically none of the new phenomena that were
novel in those models that hadn't been thought
about before — say particles, superpartners,
things like that — none of that has been
discovered, right?
I think that's what she's saying.
Now, it is true that in the neutrino sector
there is... so we didn't know whether neutrino,
something called neutrino oscillations occur,
and we've since discovered those, and those
kinds of phenomena in the neutrino sector
do suggest physics beyond the Standard Model.
But we haven't directly been able to probe
that physics yet.
Do you agree with my summary?
>>Sabine: Yes, that's correct.
So the theory for the neutrino masses also
goes back to the 1950s, so that's also not
a new thing.
But it is correct, of course, when you say
that once you know that the neutrinos have
masses, you know that there has to be something
more than the Standard Model.
And that, I think, is a solid argument.
It's just that you don't know where the new
phenomena are supposed to appear.
>>Steve: Yes.
>>Sabine: You can only tell it's very similar
with quantum gravity.
It has to be at the latest, I don't know,
two orders of magnitude below the Planck scale
or something like this, so it's ridiculously
high basically.
So if we build that new collider, we will
not be able to scan that whole parameter space.
It's way beyond what we can possibly do.
>>Steve: Right.
So another way of saying this is, that the
things that we know are out there that we
still don't understand but we know they're
out there, it is very possible this next hundred-billion
dollar collider won't tell us very much about
those mysteries that we know of already, and
so, you know, want to spend the money elsewhere.
But can I refine your question a little bit
and ask, imagine that the 100 billion or 50
billion dollars was coming.
If they didn't build the next huge machine
in China or wherever, instead of that money
being freed up to do dark matter or dark energy
experiments or quantum information experiments,
imagine it went into building missiles.
As a veteran of the efforts to save the US
super collider back in the '90s, people were
very optimistic — sorry, the enemies of
the super collider made arguments saying it
should not be built and, of course, there
are these experiments in condensed-matter
physics or in biology that'll be much better
than use of the dollars than the super collider
— but when the super collider was killed,
the money didn't show up in science budgets,
it showed up in completely, what we would
consider useless budgets.
And so in that scenario, would you still favor
building the next big collider?
>>Sabine: Yeah, so I constantly hear this
argument, I call it the zero-sum argument.
So that's an argument that every particle
physicist I know has offered me at some point.
I think it's a pretty stupid argument for
the following reason: it does nothing to explain
why the next bigger collider is a good thing
to do, right?
It basically says well, but if we don't get
the money you might not get it either, so
shut up.
>>Steve: Yeah.
>>Sabine: And so I don't think that's convincing.
[laughs]
>>Steve: The version of the argument that
you just gave, I think you know, obviously
I don't support that version of it.
I think the sort of realist attitude is, we
have this very big consortium of particle
people, and we think we can extract another
50 billion or 100 billion from mainly the
Chinese government, I think, to further advance
our subject.
The exact gain or return on that investment
is unknown at this point, and you can make
arguments either way whether it'll be good
or bad, it'll be a good ROI or not But we
are set up to extract that next project, so
let us do it — I think that's sort of more
their argument — and if we don't succeed,
it doesn't mean that you're gonna get the
money.
>>Sabine: Yeah, so I don't expect to get the
money [laughter], trust me.
So look, I think what you may be trying to
say is that there are a lot of factors that
will enter this decision that have very little
to do with the science, you know: there's
national interest, there's international competition,
there are lots of political aspects, you know,
maybe the Chinese want some shiny project
and they think that building a collider is
the thing to do, maybe it all depends on who
knows whom in which ministry or who had a
beer with whom last summer, something like
that...
So that's all possible, but those are all
aspects that I really can say nothing about.
I can really only speak about the scientific
potential, and to some extent about the technological
situation.
And I think if you look at this, it's just
not going to be a good investment.
There are better things that you could invest
in at the moment.
>>Steve: I think it's back to those inexplicable
humans and their weird hijinks.
[laughs] Yes, a big part of it would be sort
of national pride, or the Chinese wanting
to be at the forefront of what at least used
to be a super high-prestige area of science.
I don't know if it will be in the future.
Another justification for big high-energy
physics has always been that, by having very
lofty goals, like discovering the fundamental
laws of nature, you attract a lot of talent
into the field that is idealistic and wants
to work on these problems.
So you kind of, it's almost like building...
you have to build a big pyramid to get a lot
of people engaged in an effort.
And maybe the most beneficial things that
come out of it won't be the actual — certainly
not in practical terms — the particle physics
knowledge, but getting these people together
to solve huge compute problems, or transfer
large amounts of data around, might lead to
the worldwide web or some other thing which
affects the rest of the world.
And so that's kind of another argument for
why you might want to build this big pyramid
which isn't very practical, but the sort of
side consequences of building that pyramid
more than justify the cost.
>>Corey: That sounds like this actually will
create an enormous distortion in human capital,
right?
You're going to create this project that you're
not sure is gonna have any benefits, suck
a lot of very talented people in this area,
and perhaps even take them away from doing
more productive things with their...
>>Steve: Right, so this is a very subtle claim.
The claim is that you do something which is
impractical but very beautiful, very attractive
to bright young people.
They devote their lives in a monastic way
— the way that Sabine and I have for our
early decades of our lives — and yeah, maybe
the practical use of knowing about quantum
gravity is going to be very limited for hundreds
of years for humans.
However, the fact that so many people worked
so hard on this means that they solved a bunch
of other technological problems along the
way, and the spin-offs from those — I think
you could make a pretty strong argument about
this in the past, I'm not saying it will continue
to be true in the future — but that the
side consequences more than justify the amount
of money spent.
>>Corey: What I'm going to say is, I think
the natural critique of that is that's similar
to putting a distortion to the economic system
in other areas, where you're taking human
capital that can be doing other productive
things, could be creating new imaging machines
to help cure cancer perhaps...
>>Steve: I mean, if you believe in homo rationalis
and you're an economist, you maybe don't understand
this argument.
But if you realize that humans really are
under the tyranny of aesthetics, okay...
So if you talk to a brilliant 19 year old
and you say, what do you want to do, he doesn't
say, I want to make the TeV 10% better; he
says, I want to discover the secret of quantum
gravity.
And so you have to take that into account,
an aspect of human psychology.
>>Corey: I think no one's not taking that
into account.
But the general point is that there are opportunity
costs, and that the people you're attracting
to this pursuit could be doing other highly
productive things, and you may just be attracting
them with this fetishization of aesthetics,
when in fact they could be spending their
time maybe working on other fundamental things
that, had you not hung this enormous dollar
sign in front of them and talked about aesthetics,
they wouldn't be diverted from.
>>Steve: Well no, it's not the dollar sign.
The dollar sign is bringing the physicists
to, say, Wall Street.
The aesthetics are bringing them to CERN.
>>Corey: Well no, the dollar sign is building
this new collider, right?
So you have this fancy machine, you can pursue
these very, very beautiful topics, and that
may divert you from doing something else.
I mean, as Sabine's been saying, it's quite
possible you build this very large machine
and nothing is found.
And although there may be side results of
this, you still have taken, you know, smart
person 'A' who could have gone into a field
that may have actually produced some concrete
results, and send them into the field and
say, well, there may be some side spin-offs
that are successful.
So I'm just saying, any sort of person who
is more of a free-market oriented person as
far as knowledge creation or economics, would
find this presents a huge distortion of human
capital, right?
>>Steve: I think it's not as simple as you
describe it.
So to give you an example, I know many people
from my generation who left physics — often
against their will, but maybe not always — and
went into finance; and so in terms of, if
you were an economist and you said what was
their contribution to GDP, it was ginormous,
because the amount of taxes they pay every
year dwarf what any university professor pays,
okay, just the taxes.
But if you actually ask them, looking back,
well, did I create value for society, do I
feel like I got a lot dumber doing this stuff?
— yes, yes.
>>Corey: And society feels that way too about
many people, about these talented people.
That's another distortive phenomenon.
Finance was another distortive effect on the
human capital market.
>>Steve: Okay, you could take another example
— not finance, but they went into some applied
area of research, but they were kind of bored
by it, and weren't as, didn't realize their
full potential as minds, because they were
kind of doing something else but ultimately
weren't that passionate about it, so...
To answer the question of which of these two
regimes outperforms the other, you have to
fix a certain set of parameters, and we don't
really know the values of those parameters.
>>Sabine: On this issue of spin-offs, that's
certainly a possibility, but this is again
an argument that is not specific to building
a larger collider.
You can make a similar argument about other
large-scale experiments where you hire a lot
of smart people and actually give them the
time to think.
And so if that's what you want to achieve,
then you might as well invest that money in
the most promising experimentable.
And that's also if you look at particles,
for instance, you say you have this benefit
that you have smart people and they have time
to think, and who knows what they will come
up with — congravity or something.
Well, it's not working, as we have already
discussed.
The only thing they come up with is predictions
that are wrong.
>>Steve: One view of that is just that there
is some low-hanging fruit that's relatively
easy to pick, and then, you know, when you
confront something ultimately as hard as quantum
gravity and you don't have the right experimental
tools, you know, one might expect that theorists,
theoreticians would tread water for really
a long time without good experimental probes
of quantum gravity.
Do you have an opinion on that?
>>Sabine: Yeah sure, so that's certainly true,
the easy things get done first.
And you expect progress to slow down — that
I think is natural — but it doesn't really
explain why theorists make all those wrong
predictions and continue to make them without
actually changing their methods.
So that's the thing: they've been using the
same methods to make predictions ever since
the completion of the Standard Model, and
the only thing they've gotten when they went
out to actually test those predictions are
non-results, so it did not work out — but
they still haven't gotten the message, they're
still doing the same thing.
And I think there's something fundamentally
broken in that system, that they're not learning
from their failure.
>>Corey: So I think this was actually a very
interesting part of your book, the way you
believe that the scientific method has been
sort of damaged by this focus on naturalness
and aesthetics, that physicists we think of
as extremely rational and dedicated to kind
of carrying out science in its most precise
way are in fact not following the method.
If you could elaborate on your critique and
how you think they've deviated from scientific
method?
>>Sabine: Yeah, it's not only arguments from
naturalness, it's generally this method of
developing models by paying attention to criteria
from beauty.
As I already said, naturalness is not the
only criteria, and you also have this belief
that it has to be simple in an absolute way,
and there's also a lot of attention been paid
to it having a lot of symmetries, just because
that has previously worked.
So it's a reasonable thing to try, you know.
In the '80s, after they had the Standard Model,
they were trying to see if maybe gradual unification
works, and there is one larger symmetry group
that is broken, and that was a reasonable
thing to try.
But they didn't learn the message — like
that didn't work, then they tried the next
larger symmetry group and that didn't work
either, and then they tried fiddling around
with the theories rather than wondering what
went wrong there.
And it's the same with those arguments from
naturalness, that we know from the cosmological
constant, for example, that they don't work.
You know, the cosmological constant is not
natural, it just isn't natural.
They have, as you already said, there's this
issue about the prior — or depending on
what interpretation of your probabilities
you use, the initial probability distribution
— that you assume, you must make this assumption
to argue that an unnatural theory is somehow
problematic, and yet there is no way to justify
this assumption.
This knowledge has kind of gotten lost.
So you know it, and I know it's there in the
literature; but a lot of people seem to have
forgotten about it, because the others, they're
just mathematical formula that you can use
to calculate how natural a theory is, where
you can just apply it.
I think what is happening here is that people
are not correcting those methods that don't
work because they can still get it published,
you know, there's no reason for them to change
their method.
It's generally accepted procedure, everyone
does it.
They think it's good science.
>>Steve: So I think you touched there on the
issue of local incentives.
So what is the incentive for an individual
theorist to either completely abandon their
earlier research program and start something
new, or just kind of incrementally keep publishing
the papers and get the next promotion, keep
their grant money flowing to fund their graduate
students.
And so I think it's no surprise that there's
sort of psychological or institutional inertia
in those incentives.
So even though I think any thinking person
— and maybe this is usually the younger
people entering the field — would say hey,
naturalness doesn't work, it actually misguided,
it caused tens of thousands of papers to be
written over the last 30 years that turned
out to really have nothing to do with TeV-scale
physics; so we should just kind of abandon
it and loosen up and just maybe take the prior
that we don't know anything about the probability
distribution for the parameter space.
If that were the case, would you then say
the scientific method is kind of operating
okay, or are there other issues that you could
point to?
>>Sabine: So, certainly that would be progress,
and I think it's right what you say, that
the young people are going to bring in change,
because they just see that this didn't work
and they don't want to waste the time of their
life making the same mistakes as the previous
generation.
I kind of hope that now that the data, I think,
is pretty clear and says well, that does not
work, they will eventually be forced to give
it up.
But now the thing is that — unless they
figure out what was the underlying cause of
the problem, why could it be that all those
ten thousand people believed in the same nonsensical
thing — the problem is bound to recur in
some other form.
You know, they might throw out naturalness
as a stupid criterion, but they will come
up with a new stupid criterion and then use
that to fabricate their models for the next
larger collider, and then they build the collider
and they don't find anything.
It's the self-reflection that I'm missing
here.
They don't seem to really have an awareness
of what went wrong.
>>Steve: Yeah, I agree with you, there should
be some meta-learning about this, but it's
just hard for people to do it.
I would actually point to some — again,
the mysteries of humanity — some fundamental
psychological herd mentality that people have,
that if you enter a field and everybody else
is agreeing that yes, X is a right way for
model selection, you just, it's very difficult
to be a maverick and reject that in the face
of everybody else's acceptance of that idea.
And so that's why I think if you look at the
historically really great scientists, they
often tend to have this very maverick nature,
or some ability to resist social pressure
makes them an oddball in human society, but
it makes them more able to reject a herd mentality
in their own discipline.
>>Sabine: Yes, I think that's certainly true,
but it's also true that we know of that problem,
right?
And so I think that the way that scientific
research is currently organized, it makes
those problems worse rather than make them
better, for example, by giving people an easy
opportunity to get out of the field if they
feel that this is really not leading anywhere
and they're just wasting their time.
And that's, presently it's pretty much impossible
to do.
You will know that yourself, you know: if
you've done your PhD on a certain topic and
you did your first post doc on that, you're
pretty much stuck, because no one's going
to hire you to work on something entirely
different.
You can't get any grants either.
You will basically be forced to convince everyone
else that what you're doing on is the right
thing to do, and chances are you will also
come to believe it yourself.
And so there are just systemic problems with
the way that we currently organize research
that we could solve, but we don't.
>>Steve: I agree with you.
I mean, I'm an example of somebody who switched
fields on multiple occasions, and every time
is extremely hard, so I have scars all over
my, at least my psychology, from each time
that I've switched fields.
But in a way I think the problem that you're
describing is kind of similar to, in financial
markets, the problem that you will all the
time have bubbles.
And there will even be people inside pointing
to the bubble and saying hey, houses are totally
overpriced, this is insane.
But they're kind of helpless to correct the
bubble, and then suddenly you have a kind
of catastrophe and then everyone says well,
I believed that it was a bubble too, I was
never fooled.
And then we forget why we have these bubbles.
But in a way it's, to me it's a kind of difficult
thing to change about human psychology.
Corey, I think you want to say something.
>>Corey: Yeah, I think it's even perhaps a
little more extreme than that.
Again going from your book, I find your comment
about the failure to find anything but the
Higgs as the nightmare scenario.
And it seems that, if that's right, that it's
striking that people haven't absorbed that
message.
And I'm kind of curious to find out whether
you think other people in the field have sort
of, are they thinking okay, this isn't working,
I don't know quite know what to do, but I've
got to keep writing in this vein to keep my
job?
Are people aware that there's a serious problem
and just not really changing their behavior
because they're locked in their career, or
is it kind of denial?
Because it's as if the financial crisis had
happened and people just are pretending it
didn't happen.
It seems like the crisis has already occurred.
>>Sabine: Yeah, so I think the current situation
is kind of a mixture of denial — like that
that can't possibly have happened, what the
hell's going on here? — and also mixed with
hope, because the LHC will still have the
next round and maybe the particles will be
there, and everything will be good, it could
just be a more complicated version of naturalness.
Of course, I can't rule that out, maybe it's
true, right?
So there's always this hope factor.
There are also a few people, I know a few
people who have actually started working on
something different, who have stopped working
on supersymmetric models and now work on more
general models, basically — you know, some
do more astroparticle physics now than collider
physics, so there's a little bit of a change
is taking place — but yeah, as you say,
there is this amnesia that is taking place,
that people forget what they even did, and
what was going on, and "Didn't we ever talk
about the nightmare scenario?"
"No, I don't think, because it's totally great
that we have not found anything besides the
Higgs, that's teaching us so much, right?"
[laughter] And so they're kind of rewriting
history, I think — which is sad, in a sense,
because it's all documented in the literature,
of course, you know, that all those people
who've made those predictions, they can't
even be bothered to even say that yes, that
was wrong.
>>Steve: Yeah, almost no one is even fastidious
enough to just go in the literature and see
okay, who voted with their feet and spent
10 years exploring SUSI parameter space, and
was quoted as saying they were absolutely
sure we would see SUSI — I think you interviewed
such people in your book, I don't know if
they 'fessed up to what they said 10 years,
20 years ago.
But let me just comment that the discussion
we're having right now is really focused more
on the theorist community, the theoretical
physicist, because ideas like naturalness
and what is the prior on your parameter space
for a model, those are notions that theorists
are familiar with, but experimentalists who
comprise the bulk of the physics population
generally are not.
They're focused on much more practical things,
like how to really make the detector work,
or how to analyze the data.
I just want to relate a story that occurred
in this office that we're sitting in right
now.
When I first got to Michigan State, I met
with a very prominent senior ATLAS physicist,
the head of our group experimentalist here
— ATLAS is one of the big detector collaborations
here at the LHC — and when I told him, I
said well, you know, I don't feel so bad about
taking this administrative role or doing more
stuff in AI or genomics because, after all,
particle physics is in such crappy shape.
And he didn't actually understand what I meant
by that.
He literally was, he looked at me like I was
crazy, because in his mind they had completed
the construction of this ten billion dollar
machine, they had successfully got it to work,
they had discovered the Higgs boson in the
face of incredible backgrounds that they had
to suppress down by statistical analysis,
so they had accomplished a tour de force of
human scientific discovery.
And he just couldn't understand what I was
saying.
And I tried to explain to him that, well,
if we don't see anything more than the Higgs,
our field is more than likely dead [laughs]
— basically I said something like that to
him, which I think you're sympathetic to — but
he literally did not understand what I was
talking about.
>>Sabine: Yeah, it's like they walked over
the edge of the cliff and haven't yet looked
down.
>>Steve: They're taking satisfaction solving
the specific technical problems necessary
to make the experiment work, and you have
to respect that.
They're not responsible for these sort of
highfalutin ideas of theory creation and stuff
like that.
So that's the bulk of our field, actually.
>>Corey: I'd say this is actually rather consoling
to me, because I've been in a number of fields
that have almost precisely this problem, like
linguistics, where people made all sorts of
claims about theoretical linguistics is gonna
discover the innate basis of language, it's
gonna become a model for neuroscience and
cognitive science, and none of it happened.
And yet people will continue to do research
in the field using the same kinds of concepts
they did 30 years ago, and they just seem
oblivious to the fact that the field hasn't
gone anywhere.
>>Steve: But think of incentives: I make a
big claim, so I get a lot of attention, I
get a lot of resources, I become an endowed
chair professor, I win some big prizes in
my field, and I'm actually retired by the
time people figure out that my bold claims
of 20 years ago are not true.
That's a very bad system to be in, but it's
a little bit hard to change our system, like
it's hard to avoid that, because it takes
so long to verify these scientific ideas.
>>Corey: And their research program: you can
publish papers in them, you can go to conferences,
you can get grant funding, so it's like an
institutional support.
I thought this was a pathology of the things
I just happen accidentally to study as a graduate
student, but it looks like it's broader.
>>Steve: In the golden areas of physics, it
happens that the technology allows very fast
checking of the theoretical ideas, where fast
could be a couple years.
You know, in the early days of particle physics
someone would have an idea, and then very
quickly they could run the experiment and
check it.
My view is, once it becomes like, it takes
10 years to plan and build the experiment
and another 10 years to run it, that's basically
the bulk of somebody's career, and then at
that point all kinds of shenanigans are going
to be difficult to root out.
>>Sabine: You are right, of course, that experimentalists
have entirely different motivations to work
on that kind of machine.
They're happy if they get the job done, basically,
and I'm very sympathetic to that.
But I also think that they make their life
a little bit too easy, because it's perfectly
obvious that they kind of use the theorists
with their mediocre predictions to advertise
their research.
So there were all those big promises for what
the Large Hadron Collider was supposed to
find, none of which has happened; and now
the experimentalists are like, you know, they
pretend that they had nothing to do with it,
while at the same time they said nothing against
what cannot be described as other than hype
in the media.
And they still don't, right, because they're
still trying to sell now the next larger collider
with this reference to the big questions,
like what has 95% of the universe been made
of.
And this again, they pretend they didn't see
it, or I don't know.
And that's just, it's not okay.
So I blame the experimentalists for either
they didn't know what was going on, which
is bad because they should have known, or
they knew but they turned a blind eye on it.
>>Steve: I would say for most of them, they
say well, if Steve Weinberg says this is the
right way to go, I really trust this guy,
he's so brilliant, he's been right so many
times in the past, let's just do what he says;
and meanwhile I've got this horrible problem
of actually how to miniaturize these electronics
and get them to be radiation resistant so
they'll run in the detector.
I guess I feel more of the blame should go
on the theory community than on the experimental
community.
But I do agree with you that we're basically
in a pickle right now in particle physics.
And the thing that I've been watching for
a long time, really since I was a young professor,
is the sort of bleeding off of the best talent
away from our discipline and into other disciplines.
And, you know, my son is 13 now, and he's
pretty good at math and...
I would probably advise him to work on AI,
not necessarily — well, of course it all
depends on what he's interested in — but
physics doesn't seem like a discipline right
now that's really charging forward.
Now maybe some areas like quantum computation
and quantum information are poised to make
some big breakthroughs, but particle physics
to me doesn't seem like it's in a particularly
good state.
>>Sabine: Yeah, I agree with that.
>>Corey: How do you go forward now?
I mean, you're still a theoretical physicist.
With your awareness of the kind of biases
in the field, what lessons have you taken
for your research to try to avoid getting
sidetracked by concepts you think are kind
of damaging research?
>>Sabine: Yeah, so that's a very interesting
question.
So one thing is, of course, that in my own
research I try to avoid relying on arguments
from beauty.
I will admit I did use them in the past, so
it's not like I'm a saint or something, I
had to learn the lesson too.
One of the reasons why I now work on dark
matter, for example, is that there you don't
rely on those naturalness arguments, you actually
know that there is something that needs explanation,
so for me that's kind of on the safe side.
I also, so for a long time I worked on the
phenomenology of quantum gravity.
I already mentioned that, because I think
that in that case one has a really well-defined
problem.
I'm no longer working on that just basically
because I couldn't get funding, but I still
think that it's a good problem to work on.
And I'm also thinking about other areas where
arguments from fine-tuning come in, if you
know there's something to be learned from
it.
So I've recently been reading a lot of papers
about inflation — so that's the space in
the early universe that we believe led to
an exponential increase of scales — and
it is usually motivated by arguments from
fine-tuning, which is very, very similar to
arguments from naturalness.
And I've been trying to make my mind up about
whether that's a theory that one can trust
or not — and it's complicated, let me summarize
it that way.
I don't want to get into it too much, but...
So it's certainly something that has influenced
my own thinking, this inflection of arguments
from beauty.
Yeah, so for what this issue is concerned
with the social reinforcement and the cognitive
biases, I try to do what I can.
When it comes to emergent sociological trends
in the community, there is really nothing
that an individual can do something about.
But you can certainly try to avoid obvious
mistakes, like making arguments from authority
— like you just said, "If Weinberg said
it, then certainly there must be something
to it" — so that's just an argument that,
you know, raises an immediate red flag, where
I would say well, don't make it.
To some extent, I think you can learn to become
more aware of those pitfalls of logical argumentation.
I try to do that, you know.
I'm probably not the best person to judge
myself, [laughs] but I'm trying.
>>Steve: If I could make a comment on inflation,
I think I agree with you that whether inflation
"solves" certain problems in cosmology depends
a lot on your, again your prior belief on
initial conditions and arguments about entropics,
what is the most likely state of the early
universe.
So I think you're actually asking reasonable
questions there.
But for Corey's sake I would say that, if
it turns out that inflation is correct — and
there are actually non-trivial predictions
from inflation which have now been confirmed
in our observations on the Cosmic Microwave
Background — if that turns out to be true,
then you'll have a case where, in this case,
theorists in the early '80s, basically, understood
some very unbelievable phenomena that happened
just in the first instance of the universe
and actually caused the universe to have its
sort of gross morphology or gross shape, spacetime
shape.
if that's true, that would be a huge victory
of theoretical physics — I mean, I'm not
saying that the inflation is right, but if
it turns out inflation is right and did actually
happen and we become convinced of that, reasonably
convinced, then that would be an example of
an incredible forward advance or victory of
really pure thought, actually, in trying to
understand what the history of the universe
was.
>>Sabine: Yeah, sure.
So as I like to say, physicists sometimes
do the right things for the wrong reasons.
I kind of suspect that inflation may be a
case like that.
It may have been conceived for the wrong reasons,
basically to solve the monopole problem — which,
if you ask me, is a problem that doesn't exist
because maybe there are no monopoles, so what's
there to solve? — and then there's the flatness
problem and also the horizon problem.
I think those were originally the three motivations
to look at inflation.
And I don't think those are good motivations.
But now this, the data situation I think actually
speaks for inflation, though I will admit
I am not able yet to make this a very convincing
argument, so it's kind of weak.
I don't think if you want to make a case for
inflation you actually need to rely on fine-tuning
arguments.
And since I think those arguments are not
good arguments, I believe that it would be
helpful for theory development if we could
focus on the sound arguments, where you don't
have to rely on this hand-waving with the
prior, stuff like that.
>>Steve: Yeah.
absolutely.
I mean, whether it solves any cosmological
problems, there's just the question of did
it happen.
There is this dynamical phenomenon that could
have happened in the early universe, and it
leads to very specific signals in the microwave
background which we seem to be observing now.
When I was a graduate student in the late
'80s and I first learned about inflation I
thought, this is amazing, incredible that
Guth and these others came up with this; but
the idea that we would ever be able to test
it, I thought, seemed just like science fiction
back in the late '80s.
But now, actually, I would say the experimental
situation is pretty strong, I would say, personally,
the evidence that we went through an era of
inflation is actually pretty strong.
Whether it actually solves any of these cosmological
problems is a separate issue.
It may be just that theories of quantum fields
in curved spacetime allow for these periods
of quasi de Sitter growth, and we happen to
have gone through one.
So anyway, so Corey, I would say it's not
at all the best of times in high-energy collider
physics, which is the glamour area of our
field where most of the money goes, but I
would say it doesn't mean that there hasn't
been progress in theoretical physics in the
last 30 or 40 years.
Even string theory — which I don't know
if we have enough time to really get into,
Sabine, I know you have, you know, very specific
opinions about it — even if string theory
turns out not to be the right theory of quantum
gravity, not to apply to our universe, it
did produce lots of really beautiful mathematics
and non-trivial insights into areas related
to physics.
You know, it's not like people have been completely
spinning their wheels.
But in the way that she describes — which
is, theorist makes prediction of new phenomenon,
new particle, and then that is verified by
experimentalists, you know, sometime in 30
years — that didn't happen.
In that sense it's been it's been a bad 30
years.
>>Corey: Yeah, I think everyone can see this
as far as string theory from the outside.
I mean, string theory's won the Fields Medal,
it's not won a Nobel Prize in physics, and
it may never, actually, it sounds like.
>>Steve: Right.
So maybe we should close by, if you want to
riff a little bit about string theory.
I know we're running out of time, but Sabine...
So you worked in quantum gravity, but primarily
on non-string models of quantum gravity, and
we could spend a whole hour talking about
the sociology of what happened with string
theory and particle physics groups and how
it took over the whole field, and maybe either
has or has not produced great results.
But maybe you can just give us as much as
you want on that.
>>Sabine: Well, I did work a little bit on
string phenomenology.
I worked on models with extra dimensions that
were largely motivated by string theory, but
I never really worked on the theory development
or something like that.
So a lot of people tend to think that I must
be a hater of string theory, but let me assure
you that isn't so.
I do think that string theory has really good
motivations.
We already spoke about quantum gravity, so
we know that we need such a theory to fundamentally
make sense of nature, and string theory is
an approach to do that.
So I think it does have really good motivations.
But then the devil's in the details, right?
So I feel like this theory has run into conflict
with experiments so many times and then had
to be fudged, that at this point it's so artificial
one can't really trust anything that comes
out of this field.
You said that yes, there have been a lot of
mathematical insights that have been derived
from string theory.
Those have also, to some extent, informed
certain parts of physics.
The people who actually work on those areas,
mostly condensed matter physics, are not terribly
enthusiastic about it — at least that's
my interpretation when I talk to them.
But yes, you're right, it's not that nothing
came out of it.
There have been, a few things have been coming
out of it, but what has come out of it really
has told us nothing about this question of
what is the fundamental theory of spacetime.
It's more general insights about the structure
of quantum field theories that have come out
of it.
>>Steve: All right, so I think we're out of
time.
I want to thank you for spending this hour
with us, and I hope we can bring you back
on the show at some point.
Would that be okay?
>>Sabine: Yeah, that would be fine with me.
>>Steve: Great.
Well thanks a lot.
Bye.
>>Sabine: Okay, I wish you a good day.
[Music]
