3 ms·
> Was ultraviolet catastrophe really an experimental inconsistency? It seems to best understood as a theoretical inconsistency: The theory predicts a diverging
by tsimionescu 5y ago
> Was ultraviolet catastrophe really an experimental inconsistency? It seems to best understood as a theoretical inconsistency: The theory predicts a diverging (infinite) value, which we know would be wrong regardless of what the experimental evidence is.
Well, that theory also predicts that the universe can't exist for very long, which is a pretty big experimental inconsistency.
> You also give the example of "the measured invariance of the speed of light in different rest frames," but Einstein claims SR was motivated by the invariance of Maxwell's equations (a theoretical consideration), not e.g. Michelson–Morley.
Well, Maxwell's equations were relatively well experimentally verified by other experiments, so there were good reasons to at least tentatively accept their prediction of a constant speed of light* in any rest frame as a given. Even if the Michaelson-Morley experiment was not big on his mind, it was still relatively clear that this type of experiment could be performed with technology already available at the time, as the speed of light had been measured with pretty good precision already for a few decades.
So, SR was not some highly speculative theory based only on extrapolating other theories, as solutions that only address BHILP but not other problems of QM/GR are currently.
* or at least of electro-magnetic radiation, not sure when it became accepted light was EM radiation relative to the SR paper
- spekcular 5y ago> Well, that theory also predicts that the universe can't exist for very long, which is a pretty big experimental inconsistency. Sure, but I don't need to appeal to this fact to know there's a problem that must be solved. The infinities are enough. > Well, Maxwell's equations were relatively well experimentally verified by other experiments, so there were good reasons to at least tentatively accept their prediction of a constant speed of light* in any rest frame as a given. Even if the Michaelson-Morley experiment was not big on his mind, it was still relatively clear that this type of experiment could be performed with technology already available at the time, as the speed of light had been measured with pretty good precision already for a few decades. But again, even if MM couldn't have been performed, Einstein still would have had good theoretical reasons (consistency with Maxwell's equations) to posit SR. And indeed, this was the path the discovery seems to have actually taken. > So, SR was not some highly speculative theory based only on extrapolating other theories, as solutions that only address BHILP but not other problems of QM/GR are currently. Sure, but this is a difference in degree, not in kind. You accept that theoretical arguments for new phenomena that are not directly testable (at present) are acceptable if they're convincing enough. The question about BHILP under this view (which I agree with) is then about how convincing the theoretical arguments are. Hossenfelder, taken literally, suggests that no theoretical arguments will ever good enough in the absence of empirical evidence.
- tsimionescu 5y ago> Sure, but I don't need to appeal to this fact to know there's a problem that must be solved. The infinities are enough. By that logic, you shouldn't believe in black holes / GR at all, right? In practice, we can always replace infinities with some arbitrarily large numbers that don't grow all the way to infinity because of yet-unknown physics (probably quantum gravity, in the case of black holes). > But again, even if MM couldn't have been performed, Einstein still would have had good theoretical reasons (consistency with Maxwell's equations) to posit SR. And indeed, this was the path the discovery seems to have actually taken. I don't think this would have been promising if the MM experiment seemed a hundred years away, and in general I don't think SR would have been as compelling in that case. I suspect we would have still had arguments about an aether if experiments on the speed of light in different inertial frames had remained beyond reach. > Sure, but this is a difference in degree, not in kind. You accept that theoretical arguments for new phenomena that are not directly testable (at present) are acceptable if they're convincing enough. The question about BHILP under this view (which I agree with) is then about how convincing the theoretical arguments are. Sure, it's a difference in degree in the end. The plausibility of having an experiment "soon" is the degree here. I don't think that Hossenfelder would argue that if an experiment is only possible 2 years from now, or maybe even 20 years from now, you shouldn't work on some theoretical subject. But, when that time horizon stretches well beyond your lifetime and the lifetime of your students, it's perhaps time to reconsider. I also know for sure she doesn't have a problem with doing theoretical research where you don't yet know how something would be testable, as long as you plan to define an experiment as well. She explains this in some detail when discussing her own work on superdeterminism - where she plans to first define a concrete model, and then come up with experiments which could invalidate that particular model - instead of giving up a priori because "there's no known way to test such a theory".
- spekcular 5y ago> By that logic, you shouldn't believe in black holes / GR at all, right? In practice, we can always replace infinities with some arbitrarily large numbers that don't grow all the way to infinity because of yet-unknown physics (probably quantum gravity, in the case of black holes). I don't see how this follows. The ultraviolet catastrophe (or other divergences) says we have to fix something, it doesn't say that we should choose a weird ad hoc fix. > I don't think this would have been promising if the MM experiment seemed a hundred years away, and in general I don't think SR would have been as compelling in that case. It probably wouldn't have been as compelling, I agree. Don't get me wrong; the gold standard is empirical evidence. But the invariance arguments and procession of mercury would be grounds for taking it seriously. Einstein's argument for the theory depends only weakly on MM. > Sure, it's a difference in degree in the end. The plausibility of having an experiment "soon" is the degree here. I don't think that Hossenfelder would argue that if an experiment is only possible 2 years from now, or maybe even 20 years from now, you shouldn't work on some theoretical subject. But, when that time horizon stretches well beyond your lifetime and the lifetime of your students, it's perhaps time to reconsider. This seems like an unnecessarily narrow view of what constitutes worthwhile physics. First, because the experimentalists are very clever, and there's no knowing what indirect tests they might propose. But mainly because, if we can make theoretical progress on an important question, why not do that (even if empirical data is not forthcoming)? This view suggests that a physicist in 1915 (or 1925, etc.) should not try to work out properties of gravitational waves, for example, which seems obviously ridiculous to me. (The direct confirmation came about 100 years later.) If the theoretical motivation for doing so is solid, why not? I agree that BHILP paradox is probably a different case, one where we might really have no shot of saying something useful theoretically. But this requires getting into the specific details of BHILP. These general statements about what is and isn't good physics because of near-future testability all seem clearly suspect.