The Case Against Big Particle Colliders

What do the @physicists think?

Sabine Hossenfelder: Backreaction: If we spend money on a larger particle collider, we risk that progress in physics stalls.

Seems like a plausible argument to me – I quit high energy physics 20 years ago and the pickings were already getting pretty thin then.

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I think she (unfortunately) has a good argument - as much as it would be nice to probe even higher energy levels than those at the LHC, it does seem like it might be a better use of funds to develop observations through other means than particle colliders. (Something like @dga471 's experiments.)

Personally I’d really like to see a larger particle collider since there’s a theory I like that (apparently) should have signatures that the future circular collider could see (but the LHC can’t quite reach). But it’s probably not worth building it just to confirm or disconfirm a theory held by, like, 2 physicists and one overly-interested-in-physics mechanical engineer. :smiley:


What I can say is that I definitely think there is still plenty of unexplored potential for high energy physics using tabletop experiments, like the one that I’m working on (ACME), where we measure the electric dipole moment (EDM) of the electron. Experiments like these cost about 10^{-3} times as much money and personnel than that of large particle colliders, yet arguably return more than 10^{-3} scientific payoff. In our last measurement of the EDM, we are probing multi-TeV physics, as a table from a paper by our theory collaborators show:

It is true that in experiments like these, the scale of new physics being probed depends more on the model you’re testing, which is why there are several alternatives. But we’re probing 3 TeV for even the most conservative theory being considered, comparable to the scale of the LHC (~13 TeV).

There are several other EDM experiments being performed (see here: EDMs Worldwide). For example an experiment to measure the EDM of the proton is being built at Yale. There are also ongoing effortss to measure the permanent EDMs of mercury, xenon, and radium, to mention a few. Each of these experiments have potential to probe physics at scales comparable to ACME. There are even efforts that have just begun to eventually probe PeV scale physics using polyatomic molecules to measure EDMs - something that is far out of reach of any proposed particle collider for the next few decades, if not centuries.

Every time I talk to theorists about EDMs, they agree that the null results we’ve been getting provides a powerful constraint on the theories they can propose. For example, here is a plot about the experimental status of supersymmetric particles (taken from Feng 2013) that we often quote in our posters:

The arrows pointing denote the region of the plot where supersymmetric particles might still possibly exist. The region is compressed upwards by the increasing scale of experiments, but also downwards by arguments from naturalness. (Notice that sleptons have basically been squeezed out of existence.) It is true that the LHC is more versatile in being able to provide limits on multiple particles (e.g. the Higgsino, Bino, Wino, etc.) whereas an experiment like ACME only provides bounds on sleptons and stop squarks. (This is because only those particles can significantly contribute to causing an electron EDM.) But ACME is currently better than the LHC at these quantities that we can probe, and since many people still believe in naturalness, this might shape expectations on what we will see at the LHC.

The funding for all of these EDM experiments combined per year probably amount to less than $100 million. (Compare that with the $1 billion/year operating budget of the LHC. This would presumably be several times higher for a 100 TeV particle collider.) I don’t know if I agree with all of Hossenfelder’s arguments, as we usually view ourselves as a complement, rather than competition, to the LHC, and the funding pool for EDM experiments is usually completely different from that of high energy particle physics. However, even $100 million/year more devoted to EDMs (or other similar tabletop experiments probing new physics) would be a game-changer for this field.


Love the names: higgsino, slepton, etc. But most especially, what is a spurion?

@dga471 this is an excellent article!

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