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Three decades have passed since the first direct search for dark matter, a modest attempt at recycling the data from a particle detector originally built for another purpose. This work was a rapid response to a proposal by theoretical physicists Mark Goodman and Edward Witten, who called attention to the possibility of detecting dark matter via nuclear recoils. The experimental approach proposed is similar to playing billiards with an invisible cue ball. If you see a colored billiard ball (an atomic nucleus in the body of the detector) suddenly veering off for no apparent reason, you know it must have been struck by something you can’t see directly (a dark-matter particle).
The hypothetical cue balls were clumped together under one witty denomination: WIMPs, for Weakly Interacting Massive Particles. This rather generic term encompasses all new particles able to produce nuclear recoils, while not partaking of other mechanisms of interaction favored by the riffraff of known particles. Experimenters proposed and implemented a large number of ingenious techniques to look for these nuclear recoils. The experiments put into practice smart new ways to accept signals originating from nuclear recoils only, while rejecting all other forms of interaction.
When it comes to dark matter, we may be having trouble accepting what nature is telling us.
With the exception of isolated searches for axion-like particles (ALPS), dark matter hunters have predominantly concentrated on WIMP detection. This devotion is not due to an unhealthy fixation on a game of microscopic billiards: WIMPs are naturally generated by, for instance, supersymmetric extensions of the Standard Model of particle interactions. Common sense dictates that we should look first for dark matter candidates enjoying a solid theoretical motivation.
It is all very sensible, but there is just one problem: It hasn’t worked. After 30 years of assaults to the WIMP high tower, no experiment has produced unambiguous evidence.
The combination of negative results from both dark matter searches and accelerator experiments has resulted in a progressive reduction in supersymmetric models able to spawn a cosmologically-relevant WIMP. Perhaps as a reaction to this, theorists have vigorously explored alternatives. The last few years have witnessed a surge of theoretical interest in alternatives to a “vanilla” medium-mass WIMP interacting through nuclear recoils. Two themes, oftentimes overlapping, can be discerned in this flurry of activity: Particles with lighter masses, incapable by virtue of their tiny momentum of producing signals above the sensitivity of present-day detectors, and an examination of interaction mechanisms other than nuclear recoils. This shift of interest can be illustrated by the last dark-matter candidate to be endorsed by Edward Witten and his modern co-conspirators: A particle so light that its wavelength would stretch the diameter of a typical galaxy.
But experimentalists have yet to change their ways—and I speak as an experimentalist myself. We are supposed to be the people with our feet firmly planted in the ground, unlike our theorist friends who float in the clouds of speculation. But when it comes to dark matter, we may be having trouble accepting what nature is telling us. In fact, most of us still take our cue from the paper by Goodman and Witten, which has collected close to 900 citations, at a monotonically increasing rate: You would think that we are just starting to pick up speed.
Unfortunately, the heavy investment of the experimental community into the next and possibly final generation of WIMP detectors has resulted in a sort of inertia, with no major searches performed in response to the ongoing phenomenological prod. Are experimentalists more patient than their theory counterparts? More narrow-minded? Is this restlessness premature? What are 30 years in the grand scheme of the cosmos? After all, it took James Chadwick more than a decade of experimentation to discover the neutron, also by looking for those pesky nuclear recoils.
Those who should be proposing new approaches to dark-matter detection see their best years pass in a blur.
The answer to these questions is multifaceted, and a good example of the complex dynamics governing the modern churning of scientific progress. One can start by naming the obvious: Building good experiments, and making them work, takes considerable time and effort. For as long as physics remains an experimental science, this fact of life will damp the response time to any theoretical input. ADHD, when properly channeled, can help augment the impact of a budding theoretician. The same syndrome in a young experimentalist will lead, with certainty, to a very brief career: We are expected to finish what we start.
But there is another, less healthy dynamic at work, for which experimentalists should acknowledge responsibility. What started as a field of small experiments, with plenty room for creativity and invention, has been infected by a malady first noticed in high-energy physics. As experiments grow in size and complexity, paths for anything smacking of originality are few and far between. Remain a loyal cog in the machine, doing your well-defined bit, and you will be, with some luck, compensated. As a result, those who should be proposing new approaches to dark-matter detection, the instrumentalists with a deeper sense of how to build the better mousetrap, see their best years pass in a blur. Even if this sad trend wasn’t there, one is left wondering how much funding would a young entrepreneurial spirit have access to at a time when the little available is fully committed to ongoing WIMP searches.
When a student considering joining a dark-matter search approaches me these days, I describe two possible scenarios. In the first, a WIMP is discovered within the reach of the next generation of detectors, and we transition to a “golden age” of dark-matter precision studies. Involving abundant funding and job security, but with most of the thrill now gone. If I were said student, arriving at this party a bit too late, this would be a mightily boring prospect, and I try to communicate precisely that. The other scenario is apocalyptic, and therefore much more satisfying. Nothing comes up in those detectors, the LHC liquidates the remaining interest in supersymmetry (at least for any reasonable person), and larger-scale WIMP searches go the way of underground proton-decay efforts a few years ago, when dominant Grand Unified Theories fell out of fashion, that is, into oblivion.
Out of those ashes, with the WIMP blinders now removed, we would regroup and retrain, coming up with a more balanced portfolio of efforts, in better correspondence to the many guises particle dark matter could take: I am personally attracted to experiments not requiring an underground site, simpler searches that in good order should have been performed up front, decades ago. If we learned our lesson, we would also do away with any theoretical bias, the often malignant “common sense” mentioned above, concentrating instead on developing new instruments sensitive to any imaginable mode of interaction from a dark sector. One can only hope.
Juan Collar is a professor at the Kavli Institute for Cosmological Studies at the University of Chicago.
Lead Image Credit: ESO
This article was originally published on Nautilus Cosmos in February 2017.
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