Sunday, February 09, 2014

Got a problem? Good for you...

Natalie Portman
Physicists love good problems, they take them out for dinner and sleep with them. Unsolved problems are
their reason d’etre. And yet it pains me considerably if somebody dismisses a paper or research project with the remark:
“Well, what problem does that solve?”
Indeed, this came up in the discussion of the workshop I attended last week, the criticism that much of current research doesn’t seem to solve any existing problem.

I agree on the underlying sentiment. Yes, most of what gets published in physics these days will almost certainly turn out to be useless to the end of describing nature. But it’s always been this way and will always be this way. It’s in the nature of trial and error that you must try and err.

I disagree though that research is only worthy if it solves, or at least attempts to solve, a known problem.

To begin with good problems don’t grow on trees. Yes, it is often the case that the solution of one problem grows up to be the next problem, ready to pick. But that isn’t always so. Sometimes you have to go and hunt them down. And many problems are found just because researchers – both theorists and experimentalists – followed their curiosity and stumbled upon something interesting. The generation of problems is so important to progress that physicists sometimes are tempted to create problems where there are none, just so they have a target for their methods. Think of superluminal neutrinos, the pioneer anomaly, or the penta-quark.

So research is clearly also important if it draws attention to a problem rather than solving one. A recent example is the black hole firewall. And really, what problem did that solve?

The biggest part of research is dedicated to finding or solving problems, but that still isn’t all of it. Some of research is failed solution attempts. Failing and sharing failure is valuable not only because it can save other people’s time, but also because a failed solution to one problem can turn out to solve another problem. The post-it glue’s failure to stick was also its success. Einstein’s “blunder” eventually turned out to have its use when we discovered the universe’s expansion accelerates. Bubble wrap was conceived as washable wallpaper. Research in string theory was originally pursued to understand the strong nuclear force.

Somebody else’s failure of yesterday might be your solution tomorrow.

And then there is just free-wheeling curiosity that is often a by-product of researchers trying to better understand their gadgets or models. It might or might not turn out to be useful for anything. These are failed attempts to find a problem, or solutions without a problem.

I too used to be cynical about the irrelevance of most papers and their failure to address existing problems. Now I think of them as exercises, as documentations of physicists learning or improving their methods. In fact, often these papers are exactly this: projects give to students or postdocs. Others are reports on somebody’s current interests and thoughts, or their progress in understanding particular relations that will or will not lead anywhere. They might have been out hunting and now want to show off what they found, even if it wasn’t what they were hoping for. Or their idea of a good problem might just not agree with mine.

In the long run, science is much better off with a diversity of interests than with the streamlined attack favored by the dismissive comment “Well, what problem does that solve?”


  1. "black hole firewall Physical theory eschews empirical falsification (no grant-funded trash cans). This is impact factor liberating! If a Kerr (spinning) black hole's mass resides in its infinitesimal radius central singularity, wherefrom art thou, angular momentum? Black hole mass equivalent is its event horizon. Falling in is "splat!" Neutrinos are charged leptons less charge. Mass a charged lepton, subtract charge and its self-energy, know all three neutrino masses.

    Opposite shoes vacuum free fall non-identically because vacuum is trace chiral anisotropic toward quarks (hadrons). Dark matter is Noether leakage, vacuum isotropy and angular momentum, thus Milgrom acceleration. Parity violations, symmetry breakings, chiral anomalies, Chern-Simons repair of Einstein-Hilbert action are not unending mysteries, they are fundamental vacuum diagnostics that vanish given a proper founding postulate. Write that up in 26 dimensions and send it off.

    Science includes Galileo. Aristotle is obviously not enough.

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  3. A powerful defense of the path less traveled and those foolish enough to venture on it.

  4. Hello Sabine,

    But even indirectly pretty much every research direction or paper can be formulated as an attempt to answer or explore a problem. Correct?

  5. Sabine: the issue is that the public have problems, and it's (largely) the public who are funding the physicists. As a case in point CERN stands for Centre European for Research Nuclear but there's no energy research going on there, even though energy is a big problem.

    Following on from that, if the public perceive theoretical physicists to be living in a bubble of intellectual arrogance on cosy fat sinecures spouting pompous irrelevance, funding will get cut.

    Do try to bear that in mind, particularly since there's been arguably no scientific progress in decades.

  6. Yes to all thoughts about research motivations or non-motivations - research for curiosity, research despite non-usability for the explanation of the nature in the end, and research for invented problems. One can add feelings and intuition to the triggers of research.

    It would be stupid to derive a request that research must always solve ready formulated problems from the fact that research is often triggered and driven by known problems. But, I claim that there are in fact always problems behind research. Research tackles the problem or say the task to increase knowledge. It would not be research otherwise.

    Therefore I think that there is always an answer to the question “Well, what problem does that solve?”. A researcher should be able to answer what knowledge he tries to achieve. And also Einstein's blunder solved a problem for him. The formulation about the blunder was made later, when knowledge had been progressed already. That the cosmological constant was then temporarily not seen as necessary and reappeared with another value much later is the normal procedure of approaching the truth. That's not an example of non-problem-driven research.

    Finally, a remark about "[...] the irrelevance of most papers and their failure to address existing problems. Now I think of them as exercises, as documentations of physicists learning or improving their methods."

    Yes, nobody can work always at the forefront of science. One has to work through existing knowledge in order to find its boundaries. Therefore, these exercises are inevitable and will provide in the best-case the ideas to push boundaries outwards. But, shouldn't we name this work not "studying" to a larger extend, and must all "lecture notes" be published as research results where they look much more like technical reports? This is probably an effect of the current research organisation as well as the largest ever number of active researchers in history who are in need of justification of their work. If funding agencies would really understand the research process, more technical reports and much thinner journal would be the way forward.

  7. What ails the arxiv is not that most papers don't solve pre-existing problems. That would be ok. If a paper brings to light some point that has not occurred to anyone, that is ok, whether a solution is proposed or not. In fact, the AMPS paper would have been vastly better if they had contented themselves with pointing out the problem with complementarity, and stopped there, without going on to talk about nonsense like firewalls.

    What is really bad is that so many papers, and indeed entire research programs, are so badly motivated. All too often you find yourself asking, "why did these people do this?"

  8. Nice article. The problem with thinking of these papers as exercises is that there are infinite ways to get something wrong or 'not even wrong'. Rather than bestowing insight, these papers serve as red herrings. In times of slow experimental progress , the overall number of papers published should reduce (at least in hep). But it seems to be quite the opposite.

  9. " As a case in point CERN stands for Centre European for Research Nuclear but there's no energy research going on there, even though energy is a big problem."

    Huh? There is no "energy" in the name of the organization. OK, it is "nuclear" and not "particle", but surely that can be put down to historical reasons.

  10. Giotis,

    No, I don't think so, unless you mean that in a trivial way. You could probably interpret literally every step you do as 'solving a problem'. Solve the problem of getting your feet out of bed, solve the problem of opening the toothpaste, etc etc.

    What I mean here is that not all of research is dedicated to solving a known open problem in physics, and I don't think it should be. Much of it is simply exploration. That is much more obvious if you think of experimental physics than of theoretical physics, but the same exists in theoretical physics. Now you can go and say you divide up this 'exploration' into small steps and call them problems (solve the problem of finding the relevant literature, solve the problem of numerically solving this equation, etc etc), but that's not 'solving a known research problem' in the sense that I referred to, and in the sense that the sentence I quote above is normally used (typically: some SM extension or modification of GR that adds pretty useless fields for no particular reason). Best,


  11. Then there are, of course, also physicists, who really attempt to solve the existing problems (and sometimes even get their papers published),but nobody cares.

  12. Two better questions might be:

    1. What question does the paper/research attempt to address?

    2. Does the paper/research generate any definitive* predictions?

    (* A definitive prediction is: prior, feasible, quantitative, non-adjustable and unique to the ideas being tested)

  13. Good point:
    "So research is clearly also important if it draws attention to a problem rather than solving one."
    Yes, finding of inconsistencies and anomalies and loose ends is worthwhile. Finding that there were infinities in QED was important, finding that certain symmetries were violated, etc.

  14. /* Well, what problem does that solve? */

    It's a priority problem - the research of findings with practical applications should be considered first. Or the mainstream physics will become separated from the further progress of human civilization (cold fusion, antigravity drives, etc..)

  15. There are two main reasons superior to all the rest for making such 'trial-and-error' papers that go beyond present establishement:
    a) Because it's fun
    b) For the Hell of it all!
    c)"Nothing is real and everything is permitted"( Hasan Ibn Sabbah )

  16. If somebody asks ‘what problem does this solve’ they are usually just trying to find out ‘what problem does this try to solve’. Adding ‘try’ would imply that the paper failed, but you'd not want to suggest this when you don't even understand what the problem is. And it's the job of the paper to clarify what is it that they try to address.

    It's rather good to pose this question, especially to oneself.

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  18. I'm not shure everybody knows this funny story:
    Hawking and WIFI

  19. Boy, Natalie Portman is hot! And my robot filter consists of four hearts in a row with "romance" superimposed; is this a Jungian synchronicity?

    There exist so many excellent examples of what you say. One of my favorite would be Herman Weyl's gauge theory; it didn't apply to General Relativity but became indispensable with quantum field theory. I also once watched a series of videos about string theory on PBS (28 videos) and in the first they interviewed the mathematician who figured out that this certain equation described an infinitesmally small string. He sent his work to a prestigious Math Journal and the editors sent it back saying essentially, "nice work but so what?" The PBS interviewer asks the mathematician, "So what did you do then?" The mathematician looked at the interviewer with the funniest look and said, "Well, I got drunk!" Of course his presence in the video is vindication. One just never really knows . . . Sometimes it takes hundreds of years as in the case of the Wronskian and often it involves tragedy as in the case of group theory . . .


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