anorlunda said:
In what ways might research in these theories become useful even the theories can't be proved?
All theories are unproven until you put substantial effort into going about proving them. So choosing unproven and unproveable theories and conjectures is a very important part of the process. On one hand, you have to identify "not even wrong" theories that aren't worth pursuing, and on the other hand, you have to acknowledge that behind every research agenda is an unproven theory, in order to recognize that there are risks into devoting all of your efforts on it without considering alternatives or trying to generate alternatives to your assumptions.
Most really bad mistakes made by smart people flow from false assumptions, not from faulty logic or flawed execution of experiments.
Probably the most useful purpose of theories that can't be proved due to the impossibility of acquiring observational evidence is that it provides researchers with intuition on what theories for which observational evidence is available are worth pursuing because of Baysean priors driven by the theory about what important problems are truly unexplained and about what further investigation is likely to reveal.
For example, if you have some pre-BB theory that makes it sensible and natural for there to be baryon asymmetry in the universe between matter and anti-matter at t=0 of the Big Bang, an investigator's perspective on whether it is sensible to invest a lot of experimental and theoretical effort into trying to devise a theory that permits violations of baryon number (which is conserved in the Standard Model) is dramatically reduced relative to an investigator who sincerely believes that baryon number at t=0 had to be zero which makes the elusive hunt for baryon number violating processes a matter of deep importance that just has to be out there.
If you think that baryogenesis and leptogenesis is a serious unsolved problem, for example, your Baysean prior about the likely viability of Majorana mass for neutrinos and Supersymmetry (both of which allow B-L conserving process that violate B and L number conservation separately) will be much more bullish and you will devote far more resources to that, than you will if you believe that finding a mechanism that violates B or L conservation is unimportant given the resources that have already been devoted to the problem when you have already done some pretty serious searches that have failed to find it.
If you see a natural reason for the Higgs boson to have the mass that it does, even if it is unproveable with observational evidence, you are far less likely to make finding solutions to the "hierarchy problem" a priority. If you see a natural reason that is unproveable for the strong force not to have CP violation, then you're probably not going to devote a lot of evidence to investigating the possibility that axions exist.
An immense amount of resource allocation in physics is based upon Baysean priors and intuition about what phenomena are likely to be out there to be discovered which is based upon unproveable theories and unproven conjectures and perspectives about what is natural. These meta-theories have immense real world budgetary, staffing, and personal research agenda setting impact, and so research into these theories in order to find meta-theories that are useful because they set research priorities that turn out to be fruitful are useful even if they themselves can't be proven, while unproveable theories that tend to set research priorities that turn out not to be fruitful can do immense harm even though no one ever claimed that the theories could be directly proven or were proven.
Hypothesis generation is a critical part of business of scientific discovery and that part of the process is driven by intuition, conjectures, unproveable theories, Baysean priors, and the sociology of the discipline. But, since they have immense real world effects, we need to be more transparent about these assumptions so that they can be challenged and so that we can think more clearly about how to evaluate if we are generating the right kinds of hypothesizes and if we are falling into the perils of group think.
We have more well trained scientists alive today, with more resources, than at any time in the history of science. But, I fear that we are squandering an unreasonably large share of these vast resources, because group think and bad meta-theories that cannot be proven or are mere conjectures, are diverting a huge share of these resources in directions that are not fruitful or duplicative, in a manner resembling the Middle Ages when centuries of the best talent in Europe was squandered on what ultimately turned out to be a scholastic theology and Platonism based research agenda that ended up being worthless because its foundation was inherently flawed, even though its axioms seemed reasonable and attractive enough to become the group think of academia and the intelligensia for centuries. Even Newton straddled that divide, devoting as much of his immense insight and time to Unitarian theology that has long since been forgotten and made no difference to future generations, and to alchemy based upon Platonic ideals rather than the Aristotelean ideals of real chemistry, as he did to physics and calculus where he almost single handedly created classical physics, classical graviation theory, and calculus.
To go ahead and name names, I think that our current physics establishment has far too many of its eggs in the baskets of string theory, supersymmetry, and the particle based dark matter hypothesis, and far too few of its eggs in other research programs such as investigating the implications of QCD and GR in complex systems, in modified gravity theories to explain dark matter hypotheses, and it other fundamental physics theory programs. It isn't that string theory, supersymmetry, and particle based dark matter theories don't deserve investigation and development, but these research programs should have perhaps a third or less of the resources devoted to them that we see today, and the balance of our scientific resources should be devoted to other research programs.
String theory and its cousins have been driven too strongly by Platonic premises about beauty and naturalness, that are philosophical in origin, which in hindsight, decades later, seem to have been asking some of the wrong questions. We have overestimated the usefulness of these unproven conjectures and metatheories to our detriment. (This isn't to say that the string theory program has left us entirely empty handed, but it has hardly been a bargain for the percentage of theoretical physics and SUSY chasing HEP resources that we have thrown at it.)
For example, the agenda of rigorously establishing the laws of nuclear physics using first principles from the Standard Model is a difficult but doable project that has sat on the shelf for half a century because no one was been willing to devote the research resources to take it on for fear that they would miss out on the next great thing in string theory.
Since we can't determine a priori which set of conjectures and unproveable theories should drive our research agenda, we need to be transparent about what those assumptions are and then intentionally diversify and isolate groups working on different agendas in order to avoid group think and to put our eggs in more than one basket. Lots of those baskets will come up empty. But, our odds of getting a winner somewhere on big breakthroughs would be greater if we had a more balkanized research community.
