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I know you all wanted me to say something about the question of whether or not to build
a new particle collider, one that is larger than even the Large Hadron Collider.
And your wish is my command, so here we go.
There seem to be a lot of people who think that I’m an enemy of particle physics.
Most of those people happen to be particle physicists.
But this is silly, of course.
I am not against particle physics, or against particle colliders in general.
In fact, until recently, I was in favor of building a larger collider.
Here is what I wrote a year ago: “I too would like to see a next larger particle
collider, but not if it takes lies to trick taxpayers into giving us money.
More is at stake here than the employment of some thousand particle physicists.
If we tolerate fabricated arguments in the scientific literature just because the conclusions
suit us, we demonstrate how easy it is for scientists to cheat.
Fact is, we presently have no evidence – neither experimental nor theoretical evidence – that
a next larger collider would find new particles.”
And still in December I wrote: “I am not opposed to building a larger collider.
Particle colliders that reach higher energies than we probed before are the cleanest and
most reliable way to search for new physics.
But I am strongly opposed to misleading the public about the prospects of such costly
experiments.
We presently have no reliable prediction for new physics at any energy below the Planck
energy.
A next larger collider may find nothing new.
That may be depressing, but it is true.”
Before I tell you why I changed my mind, I want to tell you what’s great about high
energy particle physics, why I worked in that field for some while, and why, until recently
I was in in favor building that larger collider.
Particle colliders are really the logical continuation of microscopes, you build them
to see small structures.
But think of a light microscope: The higher the energy of the light, the shorter its wavelength,
and the shorter its wavelength, the better the resolution of small structures.
This is why you get better resolution with microscopes that use X-rays than with microscopes
that use visible light.
Now, quantum mechanics tells us that particles also have wavelengths, and for particles higher
energy also means better resolution.
Physicists started this with electron microscopes, and it continues today with particle colliders.
So that’s why we build particle colliders that reach higher and higher energies, because
that allows us to test what happens at shorter and shorter distances.
The Large Hadron Collider currently probes distances of about one thousandth of the diameter
of a proton.
Now, if probing short distances is what you want to do, then particle colliders are presently
the cleanest way to do this.
There are other ways, but they have disadvantages.
The first alternative is cosmic rays.
Cosmic rays are particles that come from outer space at high speed, which means that if they hit
atoms in the upper atmosphere, then that collision happens at high energy.
Most of the cosmic rays are at low energies, but every once in a while one comes in at high
energy.
And the highest collision energies still slightly exceed those tested at the Large Hadron Collider.
But it is difficult to learn much from cosmic rays.
To begin with, the highly energetic ones are rare, and they happen far less frequently than
you can make collisions with an accelerator.
Few collisions means bad statistics which means limited information.
And there are other problems, for example we don’t know what the incoming particle
is to begin with.
Astrophysicists currently think that it is a combination of protons and light atomic nuclei, but really
they don’t know for sure.
Another problem with cosmic rays is that the collisions do not happen in vacuum.
Instead, the first collision creates a lot of secondary particles which collide again
with other atoms and so on.
This gives rise to what is known as a cosmic ray shower.
This whole process has to be modelled on a computer and that again brings in uncertainty.
Then the final problem with cosmic rays is that you cannot cover the whole surface of
the planet to catch the particles that were created.
So you cover some part of it and extrapolate from there.
Again, this adds uncertainty to the results.
With a particle collider, in contrast, you know **what** is colliding and you can build
detectors directly around the collision region.
That will still not capture all particles that are created, especially not in the beam
direction, but it’s much better than with cosmic rays.
The other alternative to highly energetic particle collisions are high precision measurements
at low energies.
You can use high precision instead of high energy because, according to the current theories,
everything that happens at high energies also influences what happens at low energies.
It is just that this influence is very small.
Now, high precision measurements at low energies are a very powerful method to understand short
distance physics.
But interpreting the results puts a high burden on theoretical physicists.
That’s because you have to be very, well, precise, to make those calculations, and making
calculations at low energies is difficult.
This also means that if you should find a discrepancy between theory and experiment,
then you will end up debating whether it’s an actual discrepancy or whether it’s a
mistake in the calculation.
A good example for this is the magnetic moment of the muon.
We have known since the 1960s that the measured value does not fit with the prediction, and
this tension has not gone away.
Yet it has remained unclear whether this means the theories are missing something, or whether
the calculations just are not good enough.
With particle colliders, on the other hand, if there is a new particle to create above
a certain energy, you have it in your face.
The results are just easier to interpret.
So, now that I have covered why particle colliders are a good way to probe short distances, let
me explain why I am not in favor of building a larger one right now.
It’s simply because we currently have no reason to think there is anything new to discover
at the next shorter distances, not until we get to energies a billion times higher than
what even the next larger collider would reach.
That, and the fact that the cost of a next larger particle colliders is high compared
to the typical expenses for experiments in the foundations of physics.
So a larger particle collider presently has a high cost but a low estimated benefit.
It is just not a good way to invest money.
Instead, there are other research directions in the foundations of physics which are more
promising.
Dark matter is a good example.
One of the key motivations for building a larger particle collider that particle physicists
like to bring up is that we still do not know what dark matter is made of.
But we are not even sure that dark matter is made of particles.
And if it’s a particle, we do not know what mass it has or how it interacts.
If it’s a light particle, you would not look for it with a bigger collider.
So really it makes more sense to collect more information about the astrophysical situation
first.
That means concretely better telescopes, better sky coverage, better redshift resolution,
better frequency coverage, and so on.
Other research directions in the foundations that are more promising are those where we
have problems in the theories that do require solutions, this is currently the case in quantum
gravity and in the foundations of quantum mechanics.
I can tell you something about this some other time.
But really my intention here is not to advocate a particular alternative.
I merely think that physicists should have an honest debate about the evident lack of
progress in the foundations of physics and what to do about it.
Since the theoretical development of the standard model was completed in the 1970s, there has
been no further progress in theory development.
You could say maybe it’s just hard and they haven’t figured it out.
But the slow progress in and by itself is not what worries me.
What is worries me is that in the past 40 years physicists have made loads and loads
of predictions for physics beyond the standard model, and those were all wrong.
Every.
Single.
One.
Of them.
This is not normal.
This is bad scientific methodology.
And this bad scientific methodology has flourished because experiments have only delivered null
results.
And it has become a vicious cycle: Bad predictions motivate experiments.
The experiments find only null results.
The null results do not help theory development, which leads to bad predictions that motivate
experiments, which deliver null results, and so on.
We have to break this cycle.
And that’s why I am against building a larger particle collider.