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.
