Which problems make good research problems?

mini-problem [answer here]

Scientists solve problems; that’s their job. But which problems are promising topics of research? This is the question I set out to answer in Lost in Math at least concerning the foundations of physics.

A first, rough, classification of research problems can be made using Thomas Kuhn’s cycle of scientific theories. Kuhn’s cycle consists of a phase of “normal science” followed by “crisis” leading to a paradigm change, after which a new phase of “normal science” begins. This grossly oversimplifies reality, but it will be good enough for what follows.

Normal Problems

During the phase of normal science, research questions usually can be phrased as “How do we measure this?” (for the experimentalists) or “How do we calculate this?” (for the theorists).

The Kuhn Cycle.
[Img Src: thwink.org]

In the foundations of physics, we have a lot of these “normal problems.” For the experimentalists it’s because the low-hanging fruits have been picked and measuring anything new becomes increasingly challenging. For the theorists it’s because in physics predictions don’t just fall out of hypotheses. We often need many steps of argumentation and lengthy calculations to derive quantitative consequences from a theory’s premises.

A good example for a normal problem in the foundations of physics is cold dark matter. The hypothesis is easy enough: There’s some cold, dark, stuff in the cosmos that behaves like a fluid and interacts weakly both with itself and other matter. But that by itself isn’t a useful prediction. A concrete research problem would instead be: “What is the effect of cold dark matter on the temperature fluctuations of the cosmic microwave background?” And then the experimental question “How can we measure this?”

Other problems of this type in the foundations of physics are “What is the gravitational contribution to the magnetic moment of the muon?,” or “What is the photon background for proton scattering at the Large Hadron Collider?”

Answering such normal problems expands our understanding of existing theories. These are calculations that can be done within the frameworks we have, but calculations can be be challenging.

The examples in the previous paragraphs are solved problems, or at least problems that we know how to solve, though you can always ask for higher precision. But we also have unsolved problems in this category.

The quantum theory of the strong nuclear force, for example, should largely predict the masses of particles that are composed of several quarks, like neutrons, protons, and other similar (but unstable) composites. Such calculations, however, are hideously difficult. They are today made by use of sophisticated computer code – “lattice calculations” – and even so the predictions aren’t all that great. A related question is how does nuclear matter behave in the core of neutron stars.

These are but some randomly picked examples for the many open questions in physics that are “normal problems,” believed to be answerable with the theories we know already, but I think they serve to illustrate the case.

Looking beyond the foundations, we have normal problems like predicting the solar cycle and solar weather – difficult because the system is highly nonlinear and partly turbulent, but nothing that we expect to be in conflict with existing theories. Then there is high-temperature superconductivity, a well-studied but theoretically not well-understood phenomenon, due to the lack of quasi-particles in such materials. And so on.

So these are the problems we study when business goes as normal. But then there are problems that can potentially change paradigms, problems that signal a “crisis” in the Kuhnian terminology.

Crisis Problems

The obvious crisis problems are observations that cannot be explained with the known theories.

I do not count most of the observations attributed to dark matter and dark energy as crisis problems. That’s because most of this data can be explained well enough by just adding two new contributions to the universe’s energy budget. You will undoubtedly complain that this does not give us a microscopic description, but there’s no data for the microscopic structure either, so no problem to pinpoint.

But some dark matter observations really are “crisis problems.” These are unexplained correlations, regularities in galaxies that are hard to come by with cold dark matter, such as the Tully-Fisher-relation or the strange ability of dark matter to seemingly track the distribution of matter. There is as yet no satisfactory explanation for these observations using the known theories. Modifying gravity successfully explains some of it but that brings other problems. So here is a crisis! And it’s a good crisis, I dare to say, because we have data and that data is getting better by the day.

This isn’t the only good observational crisis problem we presently have in the foundations of physics. One of the oldest ones, but still alive and kicking, is the magnetic moment of the muon. Here we have a long-standing mismatch between theoretical prediction and measurement that has still not been resolved. Many theorists take this as an indication that this cannot be explained with the standard model and a new, better, theory is needed.

A couple more such problems exist, or maybe I should say persist. The DAMA measurements for example. DAMA is an experiment that searches for dark matter. They have been getting a signal of unknown origin with an annual modulation, and have kept track of it for more than a decade. The signal is clearly there, but if it was dark matter that would conflict with other experimental results. So DAMA sees something, but no one knows what it is.

There is also the still-perplexing LSND data on neutrino oscillation that doesn’t want to agree with any other global parameter fit. Then there is the strange discrepancy in the measurement results for the proton radius using two different methods, and a similar story for the lifetime of the neutron. And there are the recent tensions in the measurement of the Hubble rate using different methods, which may or may not be something to worry about.

Of course each of these data anomalies might have a “normal” explanation in the end. It could be a systematic measurement error or a mistake in a calculation or an overlooked additional contribution. But maybe, just maybe, there’s more to it.

So that’s one type of “crisis problem” – a conflict between theory and observations. But besides these there is an utterly different type of crisis problem, which is entirely on the side of theory-development. These are problems of internal consistency.

A problem of internal consistency occurs if you have a theory that predicts conflicting, ambiguous, or just nonsense observations. A typical example for this would be probabilities that become larger than one, which is inconsistent with a probabilistic interpretation. Indeed, this problem was the reason physicists were very certain the LHC would see some new physics. They couldn’t know it would be the Higgs, and it could have been something else – like an unexpected change to the weak nuclear force – but the Higgs it was. It was restoring internal consistency that led to this successful prediction.

Historically, studying problems of consistency has led to many stunning breakthroughs.

The “UV catastrophe” in which a thermal source emits an infinite amount of light at small wavelength is such a problem. Clearly that’s not consistent with a meaningful physical theory in which observable quantities should be finite. (Note, though, that this is a conflict with an assumption. Mathematically there is nothing wrong with infinity.) Planck solved this problem, and the solution eventually led to the development of quantum mechanics.

Another famous problem of consistency is that Newtonian mechanics was not compatible with the space-time symmetries of electrodynamics. Einstein resolved this disagreement, and got special relativity. Dirac later resolved the contradiction between quantum mechanics and special relativity which, eventually, gave rise to quantum field theory. Einstein further removed contradictions between special relativity and Newtonian gravity, getting general relativity.

All these have been well-defined, concrete, problems.

But most theoretical problems in the foundations of physics today are not of this sort. Yes, it would be nice if the three forces of the standard model could be unified to one. It would be nice, but it’s not necessary for consistency. Yes, it would be nice if the universe was supersymmetric. But it’s not necessary for consistency. Yes, it would be nice if we could explain why the Higgs mass is not technically natural. But it’s not inconsistent if the Higgs mass is just what it is.

It is well documented that Einstein and even more so Dirac were guided by the beauty of their theories. Dirac in particular was fond of praising the use of mathematical elegance in theory-development. Their personal motivation, however, is only of secondary interest. In hindsight, the reason they succeeded was that they were working on good problems to begin with.

There are a few real theory-problems in the foundations of physics today, but they exist. One is the lacking quantization of gravity. Just lumping the standard model together with general relativity doesn’t work mathematically, and we don’t know how to do it properly.

Another serious problem with the standard model alone is the Landau pole in one of the coupling constants. That means that the strength of one of the forces becomes infinitely large. This is non-physical for the same reason the UV catastrophe was, so something must happen there. This problem has received little attention because most theorists presently believe that the standard model becomes unified long before the Landau pole is reached, making the extrapolation redundant.

And then there are some cases in which it’s not clear what type of problem we’re dealing with. The non-convergence of the perturbative expansion is one of these. Maybe it’s just a question of developing better math, or maybe there’s something we get really wrong about quantum field theory. The case is similar for Haag’s theorem. Also the measurement problem in quantum mechanics I find hard to classify. Appealing to a macroscopic process in the theory’s axioms isn’t compatible with the reductionist ideal, but then again that is not a fundamental problem, but a conceptual worry. So I’m torn about this one.

But for what crisis problems in theory development are concerned, the lesson from the history of physics is clear: Problems are promising research topics if they really are problems, which means you must be able to formulate a mathematical disagreement. If, in contrast, the supposed problem is that you simply do not like a particular aspect of a theory, chances are you will just waste your time.

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Homework assignment: Convince yourself that the mini-problem shown in the top image is mathematically ill-posed unless you appeal to Occam’s razor.