In my previous post, I made reference to the raging controversy over what’s next for particle physics, sparked in part by Sabine Hosenfelder’s argument in Lost in Math that there’s no reason to expect dramatic discoveries from a next-generation particle accelerator. In the week and a bit since that post, well, the controversy continues to rage on, with fellow Forbes blogger Ethan Siegel weighing in with lofty rhetoric, noted quantum computing physicist Scott Aaronson offering a more qualified defense, and Hossenfelder understandably expressing frustration at the whole business. This clearly isn’t going away as quickly as one might like.
As I mentioned in that earlier post, though, this is a tricky topic to write about because it’s posing a genuinely difficult question about research priorities and resource allocation. As a result, while many of the arguments for and against are delivered with great passion and conviction, I don’t find any of them fully convincing. It’s just too easy to poke holes in most of the arguments being thrown around.
The bulk of the hole-poking falls on the pro-accelerator side, because they’re employing more of a shotgun approach involving lots of different arguments thrown out in hopes that one of them hits something. None of these are completely without merit, but they’re all kind of underwhelming, and allow for really obvious “Yes, but…” replies.
The hands-down favorite argument in favor of building a next-generation accelerator is of the form “There may not be a solid reason to expect to find something, but you still might find a new particle.” This is true, but it’s also reminiscent of the old New York State Lottery slogan “Hey, you never know…” And as with the lottery, this is an argument whose worth depends greatly on the resources involved. A $2 PowerBall ticket is a fun “Hey, you never know…” for someone who already has a stable upper-middle-class income, but not such a great idea for somebody who’s just scraping by, for whom it represents a larger fraction of their working budget. In a similar way, I’m rather fond of precision measurement experiments looking for signatures of exotic physics, which face lottery-like odds of success, but those are mostly pretty cheap as such things go, maybe a few million dollars. A next-generation accelerator would run to tens of billions of dollars, and long-odds gambling with that kind of money is a very different question.
Another popular take on this puts a negative spin on the finances, arguing that yes, it would be great to fund a thousand million-dollar experiments rather than spending a billion dollars on an accelerator, but there’s no chance of that happening. Money for giant projects is separate from ordinary research grants, and if that hypothetical billion dollars isn’t spent on an accelerator, it will just disappear into a tax cut allowing tech billionaires to write off the landscaping expenses for their supervillain-style lairs on volcanic islands.
This isn’t exactly wrong, but implicitly involves doing something very stupid. That is, it’s absolutely true that if physicists gave up on a super-expensive new particle accelerator and did nothing else, the money would just disappear, but that’s not really what the anti-accelerator side is asking for. What folks like Hossenfelder are calling for is for the physics community to make a rational assessment of the relative value of different projects, and direct their efforts toward securing funding for things that will work. The idea isn’t just to pack up our toys and quit the field, but rather to direct the resources and political capital that would be spent on obtaining those hypothetical billions for an accelerator (which, remember, is not a sure thing) to instead secure funding for projects that have a better chance of paying off. It might not be possible to obtain the full amount that would be spent on a new accelerator, but it seems preposterously unlikely that there would be zero extra money available if CERN were to decide to advocate for something other than ever larger colliders and direct its considerable political resources toward securing funding for that.
Another negative argument that shows up is the “squandering expertise” argument, that if we don’t build another accelerator now, there’s a host of technical knowledge built up on the path to the LHC that will be lost and need to be reinvented whenever somebody decides to build another accelerator down the road. This doesn’t hold a lot of water, either, because the idea of restarting collider physics in the future is predicated on finding a way to reach dramatically higher energies than are currently under discussion. That’s likely to involve dramatically different techniques than are currently in use, in which case the experience developed running the LHC may be of limited utility.
More than that, though, one of the key anti-accelerator arguments is that expertise running colliders is likely to be of no future use. To take an extreme argument, if there are genuinely no new particles to discover until some energy level that’s completely implausible to generate in a controlled way– ten orders of magnitude greater than the LHC energy, say– then there’s no point in trying to preserve that specific technical knowledge. If the “desert” above the LHC energy is that vast, then collider physics is an industry at the end of its useful life, and we shouldn’t be any more anxious to preserve the accumulated knowledge of how to run particle colliders than we are to preserve decades of accumulated knowledge about how to mine coal.
Flipping things around, though, that extreme anti-accelerator argument isn’t all that plausible or effective, either. After my previous post, I got an email from Joe Incandela, who I quoted second-hand, to clarify his remarks. We exchanged a couple of emails, and he provided a list of several experimental questions regarding the physics of known particles that would almost certainly be resolved if the plan to build a 100TeV collider were followed. These aren’t anywhere near as sexy as finding supersymmetric particles would be (unless you’re weirdly fired up about the Higgs self-coupling), but they’re good solid science with a near-certain payoff.
So, it’s not really true that a new accelerator would find nothing, just that it wouldn’t be likely to find anything as dramatic as is sometimes claimed. Less dramatic discoveries can still be good and worthwhile science, though. And even if nothing surprising showed up, I do have some sympathy with Aaronson’s argument that it would be good to have an actual, solid null result before we pack it in.
At that point, it again becomes a question regarding the scale of the resources involved– is a more detailed investigation of electroweak symmetry breaking and the Higgs self-coupling worth tens of billions of dollars? Ultimately, everything turns on that, and I don’t think it’s a question with an obvious answer.
Personally, at the end of the day, I tend to think that while tens of billions of dollars is a big sum compared to most grant budgets, on a global scale, it’s actually not all that much money– a billion-ish dollars a year over twenty-odd years is something we could easily afford. It’s not a great investment, maybe, in terms of expected future economic payoff, but not everything needs to be an investment. The Standard Model is one of the greatest intellectual triumphs in the history of human civilization, and going beyond it would be similarly spectacular. It might best be viewed as an art project on the scale of global civilization, and that’s probably worth $0.20 per living human per year.
That said, I’m not hugely committed to this view, and can easily see how one might come down on the other side. It is, as I said at the beginning, a genuinely difficult question to answer, and none of the many arguments being thrown around in the recent exchanges are truly decisive.