Locklin on science

The problem with Lee Smolin and physics

Posted in physics by Scott Locklin on October 15, 2009

Lee Smolin wrote a very important book a few years ago called, “the trouble with physics.” I give Lee a lot of credit: he recognizes there is trouble with physics; thousands of men have been working on string theory since the 1980s, and have yet to make anything resembling scientific progress in the subject. On the other hand, he misses out on an obvious reason why physics is in trouble, and I feel a powerful need to correct my intellectual superior in physics.

This book came out at around the same time as Woit’s “not even wrong,” which is on a similar topic, though Woit takes a different tack. Both contain decent descriptive histories of what string theory is, and where it went pear-shaped. Both books explain the sociological and ‘economic’ forces in building up a large community of very smart people … which doesn’t function properly. Both also miss out on an important thing which is pretty obvious to people outside his field. What all quantum gravity people (Smolin and his crew of merry misfits included with the string theorists) are doing is entirely aesthetically driven. There is no reason gravity should have a quantum theory any more than a ham sandwich should have a quantum theory associated with it. There are no experimental, or even observational reasons to presume gravity has a quantum limit. It’s all aesthetics. They’re nice aesthetics, but science has no real business doing aesthetics. The image Smolin paints of his flamboyant Italian colleague waving a knife around at the idea that the universe might not live up to his aesthetic ideals is supposed to be funny, but the knife fighter is emblematic of a very serious problem. Science is about learning about how the universe works, not seeking aesthetic answers to questions that the universe isn’t asking. While many great physicists have been prey to neo-platonic grandiosity as to how the universe works, they’re not being physicists when they think like that. They’re being art critics.

Allow me to explain what I mean with some other examples from Lee’s book. In his first chapter he defines what he claims are the five great outstanding problems in physics today. I must respectfully disagree with all but his second one. The four I disagree with are essentially cosmological questions; the questions string theory (and Smolin and Rovelli’s rival idea of “loop quantum gravity”) ultimately attempt to answer. Quantum gravity may be a silly question. I’m not some kind of lone heretic in saying this: I’m stealing the idea from people much smarter than I. People like the grand old man of physics, Freeman Dyson -or perhaps better yet for credential worshippers, Phil Anderson, a man who discovered something of mind-boggling importance which is largely met with a world-weary shrug by theoretical physicists in noodle theory land. Both Dyson and Anderson agree that we may no more have a quantum limit for gravity than steam engines and other grossly macroscopic phenomena have a quantum limit. Assuming gravity does have a quantum limit may be the great intellectual folly of theoretical physics of the last 50 years. Don’t do it just because Einstein did it. Einstein was also a communist, and we know that communism was a very, very bad idea.

Smolin’s outstanding problems numbers three and four, I count as essentially the same: he thinks it is important to come up with a unified field theory that predicts fundamental constants observed in nature. Why should things work this way, besides the fact that it would make Lee and his pals happy? Again; this “problem” is an aesthetic guess how he thinks things should be. These ideas about how a “theory of everything” should be are problematic for the same reasons the idea of quantum gravity itself is problematic. While many people do indeed think the universe should have some sort of ultimate theory which can unify the particles and forces, and predict why the fine structure constant is what it is, the reasons people think such are historical and aesthetic -these reasons can not remotely be described as physics. Aesthetically, physicists like only having to remember a few things, rather than many things. You can derive everything about electromagnetism by memorizing very few simple facts; same with statistical physics. Historically, the unification of magnetism, electricity and light into one theory really was a tremendous breakthrough in human knowledge. 50 years later, all manner of practical uses were found for it.

Let us compare E&M to the most successful unification of modern times, the electro-weak theory (a unification of a force governing certain kinds of nuclear decay with that of electromagnetism). Unlike Maxwell’s equations, electroweak theory is abysmally ugly. Unfortunately for aesthetics, it does appear the universe works this way. The wise and benign god who wrote Maxwell’s equations must have contracted electroweak theory out to some perverse lesser daemon, like Loki. Comparing practical implications; 50 years from the invention of modern electrodynamics we had the creation of the modern world of AC power, radio and almost everything else involving electricity which you take for granted. 50 years from the creation of electroweak theory: there have been no technological implications. I’ll go out on a safe, sturdy limb and assert there will be none, ever. As an intellectual project, glorious electroweak theory is literally more technologically sterile than … I don’t know: Thomas Aquinas ideas on how many angels fit on the head of a pin. And electroweak theory is a smashing success compared to any kind of quantum gravity; it was motivated and verified by experiment.

As for the many outstanding problems in astronomical cosmology which Smolin collects together as the fifth major outstanding problem in physics; I find it hard to get too worked up about them, as the astronomers seem to find new “anomolies” every time they fire up a new telescope. Historically, astronomy gave us Newton’s laws, but what has astronomy done for us lately in terms of real physics? Sure, dark matter and so on are interesting and worth thinking about, and it is nice to have someone telling the telescope johnnies what to look for, but there are far more frightening lacunae in physics which should be on this list.

I’m a lowlife quant: I went to a cow college and did fairly badly for myself while I was screwing around in physics. Very few of my former colleagues will stand up for me and talk about my ultimate brilliance, because frankly, I didn’t display any. However, even a mercenary dirtbag like me can come up with a better list than Lee Smolin, or, for that matter, any physicist in the public eye today. Here is the Scott Locklin’s five most important unanswered unquestions in theoretical physics today:

  1. The fundamentals of quantum mechanics. I admit it; I stole this one from Lee Smolin. I just want to know how it works when it starts to turn into classical physics. Seriously: this is important, and it isn’t known. This is the subject I concerned myself with when I was doing physics. I made no progress at all, but I think it’s one of the things worth spending your time on. There are several small sub-fields of active research in the subject: quantum chaos and Mesoscopic physics. Maybe quantum information theory -though it’s been a long time since I’ve thought about it, and beyond Shor’s algorithm, I have read an awful lot of silly bullshit coming from this quarter. For some reason, there are not 10,000 physicists thinking about the basic question of nature, like there are in string theory. Smolin correctly identified the reason why: physics bureaucracy does not favor it.
  2. The second law of thermodynamics, chaos and the arrow of time. If you never thought about this, you will say, “yeah, whatever,” but this is important. It’s important in all kinds of places; information theory, finance, psychology, and it’s not really understood why it is so.
  3. Self-organization and emergent properties in matter. Sure, you have “nanotech” types of people (subject for another rant) trying to exploit this. Why doesn’t anyone even attempt to understand this? Ilya Prigogine won the Nobel for this; it seems to be worthy of study, and there is tons more to do. Meanwhile, armies of vast string theorists count the angels on heads of a boson.
  4. Why is life? Never mind “how does life work,” tell me why life works at all! You’re all faced with an ultimate mystery of physics every morning in the shaving mirror. Why don’t you think about it a little? Don’t wave your hands on this one; tell me what’s going on. There is obviously order here; order which can presumably be understood by mathematics.
  5. How do neural computers, aka brains work? Another problem of immense import. People are studying it; there are even good pop science books on the subject. Nobody is seriously studying it from a theoretical point of view.

I have this idea that physics, along with Western civilization in general, never fully escaped from the wandervogel era “playing indian in the woods” navel gazing of post WW-1 Europe. In fact, I think as a result, physics attracts moosh-headed people who think this sort of “looking into the mind of god” thinking is, well, acceptable, when it really shouldn’t be for a serious scientist. In the Victorian era which spawned the ideas of Maxwell and (early) Einstein, a theoretical physicist’s job was to come up with models that fit the experimental data; a physicist was a sort of mathematical phenomenologist. He was not an aesthetician, though he might create something of great aesthetic merit. An interesting observation which might be made is how physics followed many other formerly rigorous fields in to the badlands of ‘theory.’ String theory is to Victorian physics what modern Literary theory or artistic technique is to their Victorian analogs. Certainly, the modern things can be said to be more ‘sophisticated’ -but it is also more useless for understanding the world.

Smolin’s idea that more affirmative action is going to help physics is laughably insane. I’d go so far as to say this is probably a symptom of the type of mental illness which thinks doing quantum gravity is important “because it must be so,” aesthetically. Physicists did better before they were required by their Universities to engage in ritual Maoist witch hunts against racism and sexism. That’s a historical fact. Throwing away the simple, effective idea of judging physicists based on something resembling competence isn’t going to get us anywhere good.

My attempt at a solution to this social problem (and it is a social problem) is a lot more radical and frightening to people who work within the University-Industry axis of mediocrity. It is positively heretical to people who worship education as some kind of secular sacrament. To my mind, the strength of the institution you belong to is the weakness of the individual. The very idea of a University is medieval and feudalistic, or at best Industrial. You want to do real original research? Quit academia and become a free lance consultant. Smolin’s most interesting menagerie of oddball physicists did just this, so I know he’d be behind me. Smolin himself works in a very nontraditional institute funded by private industry. It’s what I have done, and freed of the bureaucratic need to churn out nonsense papers, or spend my time baking vacuum chambers, my creativity has blossomed. I’ll never be an eminence grise like Smolin in any subject, as I’m not as clever as he is, but I will likely die richer, and have enjoyed my life more than chaining myself to some horrific bureaucracy whose purpose is to crush all original thought. Do you think Kepler would have had his brilliant idea if he were rotting in a University or government observatory somewhere? I don’t, and I think if you want to be Einstein or Kepler, your path is clear, and is far away from a safe life of vegetable contentment, sucking at the public teat.

Someone needs to write a futurist manifesto of physics, because physics is no longer bringing us into the future. With apologies to F.T. Marinetti:

The universities? Government labs? Cemeteries! Public dormitories where one lies forever beside hated or unknown beings. Absurd abattoirs of play actors ferociously slaughtering each other with bureaucratic slaps, idiot journal editing blows, the length of the fought-over walls!

That one should make an annual pilgrimage, just as one goes to the graveyard on All Souls’ Day—that I grant. That once a year one should leave a floral tribute beneath the icon of Albert Einstein, I grant you that… But I don’t admit that our sorrows, our fragile courage, our morbid restlessness should be given a daily conducted drudge through the universities and neuroses of long dead physicists. Why poison ourselves? Why rot?

And what is there to see in quantum gravity except the laborious contortions of an artist throwing himself against the barriers that thwart his desire to express his dream of original research?… Admiring unification theory is the same as pouring our sensibility into a funerary urn instead of hurtling it far off, in violent spasms of action and creation.
Do you, then, wish to waste all your best powers in this eternal and futile worship of the past, from which you emerge fatally exhausted, shrunken, beaten down?

In truth I tell you that daily visits to government labs and academies (cemeteries of empty exertion, Calvaries of crucified dreams, registries of aborted beginnings!) are, for physicists, as damaging as the prolonged supervision by parents of certain young people drunk with their talent and their ambitious wills. When the future is barred to them, the admirable past may be a solace for the ills of the moribund, the sickly, the prisoner… But we want no part of it, the past, we the young and strong Futurist physicists!

So let them come, the gay incendiaries with charred fingers! Here they are! Here they are!… Come on! set fire to the government labs! Turn aside the canals to flood the universities!… Oh, the joy of seeing the glorious old frauds bobbing adrift on those waters, broken and shredded!… Take up your pickaxes, your axes and hammers and wreck, wreck the long dead academic system, pitilessly!

Links:
Lubos Motl is a righteous peckerwood for a mainstream physicist. If he reads this, he’ll probably dismiss me as an insignificant dunderhead who couldn’t make it in physics: that’s one of the reasons I like the guy; I respect a straight shooter.

Some other guy’s list of important questions; typical “quantum gravity” bias, but at least he notices some other interesting stuff I don’t bother mentioning. Some of them are literally table top physics you could do at home.

A horrible example of the psychedelic quackery that passes for “science” from the New York Times “science” page

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33 Responses

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  1. John Mount said, on October 15, 2009 at 6:00 am

    Okay, perhaps Garrett Lisi can have the Nobel Prize in String Theory? He is over 25.

    • Scott Locklin said, on October 15, 2009 at 7:13 am

      Lol; no. If anyone gets the Nobel Prize in String Theory, it will be my buddy, who is the Last Man in Berkeley, like Charleton Heston in Omega Man. Seriously; if he weren’t around, I’d really lose my marbles.

      Also: I blame you if the invitations to drink beer with physicists dry up because of this.

      • John Mount said, on October 15, 2009 at 7:16 am

        I owe a beer for baiting you. Vincent Price Last Man on Earth.

        • John Mount said, on October 15, 2009 at 7:17 am

          “I owe you a beer” (argh)

          • Scott Locklin said, on October 15, 2009 at 7:38 am

            I didn’t recognize Surfing Einstein’s name at first … I admire his originality, and his hearty amateur spirit, but his physics is dumb. I also resent his managing to grab the media megaphone because he surfs; many physicists surf. Anyway: ja, beer. Or one of them group working sessions, then beer.

            • John Mount said, on October 15, 2009 at 2:26 pm

              Oh, definitely a work session. After all Philip is only so amusing.

  2. hegemonicon said, on October 15, 2009 at 2:23 pm

    Not being a physicist, are there any other promising lines of research attempting to unite quantum mechanics and general relativity, other than quantum gravity?

    • John Mount said, on October 15, 2009 at 2:31 pm

      Well I am not a physicist either. Quantum gravity has the the additional advantage that nut jobs already are already prepared for it to “explain consciousness” in addition to unifying quantum and relativistic physics. So if wishes are horses lets go with that one.

    • Scott Locklin said, on October 15, 2009 at 8:26 pm

      Well, I generally call any sort of unification between quantum mechanics and general relativity “quantum gravity.” Loop quantum gravity is one technique which Smolin and coworkers came up with -sort of easier to follow than string theory. It’s also kind of vacuous from what I’ve heard. Basically it kind of says, if there is a quantum gravity, it will have these couple of properties, without making any interesting falsifiable predictions. Strings make predictions … at absurd untestable energies.
      I remember thinking for a while that Twistor theory was kind of interesting. I believe that was Penrose’s big thing. Wakipedia says there are a zillion others, and I’m sure there are. So sad; such massive talent wasted on something so intellectually sterile.

      It’s not even remotely my field; I built optical things and worried about what atoms were doing. I think I know a flim flam artist when I see one though. Unlike something like the Gutzwiller trace formula, which was a real breakthrough with consequences; all this appears to be folly.

      • hegemonicon said, on October 16, 2009 at 3:31 am

        I wonder if the institutions behind all this work have been built up to such a point that there’s significant pressure to NOT work on something more verifiable, as proving it all wrong could bring the whole thing crashing down.

        • Scott Locklin said, on October 16, 2009 at 6:29 pm

          While I’m not a fan of conspiracy theories, institutions have their own logic for certain.

          Mostly I think it’s a collective monomania. “But Einstein said so” has become a sort of mantra. Einstein wasn’t a god. He was a man. Even if he were not a very flawed man (and he was very flawed -he married a crazy lady, then his cousin, abandoned his children, he couldn’t decide on a country to live in and had … very questionable politics to say the least); the business of science is not in turning long dead heroes into gods. The business of science is in finding out about reality. Quantum gravity and reality are not even distant acquaintances until someone can come up with an experiment which says otherwise.

  3. Brent said, on October 15, 2009 at 3:57 pm

    I know cosmology gets all the babes, but I don’t see the appeal otherwise: there are better things to do if you want to get the attention of people outside physics.

    As an aside about Kepler, Tycho Brahe did the experiments that Kepler based his theoretical work on: what is said to have killed Tycho Brahe?

    • Scott Locklin said, on October 15, 2009 at 8:10 pm

      Etiquette? All I know is, having a gold nose from a dueling injury is very cool.

  4. hegemonicon said, on October 15, 2009 at 4:41 pm

    Ugh. If anything that is a strong argument AGAINST quantum gravity.

  5. Kuas said, on October 15, 2009 at 5:10 pm

    If string theory manages to snag a Nobel it will probably be in the literature category.

    Daniel Friedan is another noted physicist, once a leading string theorist in fact, who has said there need not be a quantum limit of GR.

    • Scott Locklin said, on October 15, 2009 at 8:15 pm

      Wow, Betty Friedan’s kid. That’s a heavy burden. Disappointing he got into quantum computers afterwords: from an imponderable to an impossibility.

  6. Nav said, on October 16, 2009 at 12:09 am

    With the qualifier that I’m both a string theorist (well sort of) and a cosmologist, I thought this was brilliant. But I have a couple of disagreements.

    First off, I think the assertion that gravity need not have a quantum limit is a little off base. Given that the right hand side of Einstein’s equation (the energy-momentum tensor) has a quantum limit, then one would expect the left hand side (~the space time curvature) to also have one. If it doesn’t, then, assuming sufficiently high energy densities exist, one would need to construct an appropriate alternative theory to describe nature in this regime. And for want of a better phrase, you might as well call this quantum gravity as well.

    Of course, I suppose it’s possible to argue that a, say, steam engine doesn’t have a quantum limit, but that rather depends on how you define such a thing. It’s true that the macroscopic degrees of freedom of a steam engine are not quantized, however it’s also true that one can build a tower of effective theories that flow smoothly into one another and that describe the behaviour of the engine on every conceivable length scale that we can test. The “flow smoothly” part is important, if that’s not true one would be stuck with theories that would be logically and experimentally incompatible.

    Now, since probing quantum gravity is technically very, very hard (the energy scales are extremely high), one can certainly argue that doing quantum gravity is a waste of time (this applies to every theory of quantum gravity, not just strings); after all, it’s not really clear that unobservable theories deserve the moniker “physics”. That’s a fair point, and I don’t necessarily disagree with it (more about this in a sec).

    I’d also agree that fundamental physics is basically useless. The odds of cosmology/particle physics and the like contributing to practical society are pretty slim. Though, with that bias, I’m not sure I’d agree with your list of 5 problems, in particular the first two. I think we understand enough about quantum mechanics and (especially) the second law, that progress here will be interesting, but of little practical value.

    I was going to launch into a long bit on why the unobservable can still be physics, but since it’s a long argument that I’m not entirely sure I believe, I’ll finish with something else (though, perhaps some other time or place…).

    I find this sociology argument insulting. I, and everyone else I know in my field, studies fundamental physics (I hate this phrase, it’s horribly arrogant, but I can’t think of a better one) does so because we find it fascinating. We don’t get roped into it. It’s not because there’s some horrible threat hanging over us if we do something else and it’s really not because we’re sheep. You might argue that it’s impractical, but so is much of intellectual endeavour. There’s a level at which in order to maximise progress, you have to let people study what they wish. It’s not the most direct way of getting useful results (and while particle physics has produced little of practical value it has produced an awful lot of technical stuff – especially math – that lies at the heart of progress in more useful areas of physics), but there’s a trade off. One might argue that as a society we invest too heavily in the esoteric, an argument I whole-heartedly agree with, but I have severe doubts that focussing of merely the practical would be much better.

    Moreover (and I’ll concede being on a limb here), there is a sense in which even the least useful of pursuits has intrinsic value. We should care about the impractical physics for the same qualitative reasons we care about art and about music and the rest of that beautiful, but useless stuff. It make life better. Or, more precisely, the value of being born human increases if we live in world full of beautiful things and a world of which we have greater and greater understanding.

    • Scott Locklin said, on October 16, 2009 at 12:39 am

      Thanks for your well written and thoughtful reply, Nav:

      Well, it might be interesting for me to take issue with why the fundamentals of quantum mechanics and the arrow of time are very interesting subjects -ones which could deeply impact ordinary life for billions of people; that would defeat my main purpose. I’ll also mention in passing I do indeed think quantum gravity as a whole falls into the realm of metaphysics, since there is no physical motivation for it: merely aesthetics. So some GR equation has a quantum limit: everything in classical physics has a quantum limit! That’s why I think quantum mechanics and the arrow of time is still interesting. My interest in the correspondence principle is in things you can measure; not things you think should be a certain way. My interest has real consequences. You ultra high energy guys forget about what happens in real dynamical systems which exist in potential wells; it’s not just an uninteresting, messy limit: it’s where really weird stuff happens.

      But my main purpose here is not to argue about my taste in problems: I’ll concede my problems are boring for the purposes of argument -they’re not well funded or manned anyway, so they’re no threat to anyone. The question remains: why are there tens of thousands of “physicists” thinking about stuff which amounts to metaphysics? Why are these people owed a living? I’m not saying they shouldn’t be allowed to study this: study what you like. I’m saying, why is humanity paying for it, rather than, I don’t know, rocket science or just math or something? What y’awl do is intellectually impressive, but the disease of quantum gravity and cosmology has taken over physics departments all over the world. This field should, to my mind, be small and obscure, rather than a zillion lemmings cleaning up Ed Witten’s lecture notes. The prestige accorded such ideas is misplaced. Imagine for a moment that there were 10,000 people studying sonoluminescence … or, say, carbon nanotubes. How did those 10,000 people get there? Wouldn’t you say that is a very large number for what may be a mysterious phenomenon, but … why such a big fraction of the total number of physicists? From there, let’s take note of the fact that at least sonoluminescence and carbon nanowhatsits are problems which are in principle soluble! It bothers me that so many of the smartest people in the world are engaged in what appears to be a grandiose glass bead game. Think about something better, please! Analog computers maybe? Sonoluminescence would be good too. Anything you can measure!

      In my more unkind moments I wonder if this profusion of quantum gravity guys is due to a lack of career risk taking. There is an obvious algorithm for getting a job in string theory. There is no algorithm for making a physical prediction which can be verified by experiment; you have to be good, you have to be lucky, and you have to be right (much like in finance). Taking this element of risk out of careers: it’s a bad thing for progress.

      • Nav said, on October 16, 2009 at 7:08 pm

        Well, I think we can agree on the statement that less money should be spent of high energy physics and cosmology. However, I’m not entirely sure about this prestige business. One might argue that the prestige afforded to many things is too great (football players for one), but prestige is not an externally imposed thing. Rather, the sociological value of enterprise is determined by some appropriate combination of what individuals think is important. You might think the study of sonoluminescence is worthy of greater accolades than string theory or cosmology, but if most people disagree… well it’s like art (again), I dislike Shakespeare, most people don’t and the prestige of William’s works is determined by the majority.

        It’s worth pointing out as well that it’s a little unfair lumping together quantum gravity and cosmology. The former is very hard to test, the latter is not. There is a great deal of cosmological data and a great deal more to come. Moreover there are many models that make predictions that may or may not be verified. There is of course, some subtle philosophical argument to be had here about weather cosmology is really science, since although we can test theories, we can’t do repeated experiments (there’s only one universe). On the other hand, evolution has this problem as well (until we find life on other planets), and I think we can all agree that Darwin was a scientist.

        Last point, for now. You’re way off base with the career thing. There may be many more jobs in string theory versus loop quantum gravity. But if you want a job, this is not the field to be in. Almost everyone I know from grad school quit or only went through one postdoc before finding something else to do. This really isn’t the case for the folks I know in condensed matter physics (for example), who have pretty much all ended up doing physics, even if in industry rather than academia. You really don’t choose to be a high energy theoretical physicist because you think you’re going to get a job. You won’t. There aren’t that many places compared to the number of incoming students each year and everyone is really smart. Moreover, and I want to stress this again, more practical physics research is a far less risky endeavour from the point of view of one’s career.

        • Scott Locklin said, on October 16, 2009 at 8:04 pm

          What I’m attempting to do here is deny quantum gravity the prestige its practitioners think it is entitled to. I would like to laugh this idea off of the face of physics. You and I both know why people think it’s important: aesthetics and because famous people said it was important, and the leaders of physics have said it was important for … something approaching a century now. The fact that nothing good has come of unification physics in that near-century ought to be an indication that this question is accorded low prestige by the universe itself. By contrast, football is pretty good training for leadership at least, and people pay to watch it, so it has more of a place in the world. I’d hire a college football player sooner than I’d hire a quantum gravity nerd to trade my portfolio: they have better spatial reasoning and rapid decision making ability. They’re also better at teamwork.

          I’m not a big fan of cosmologists; you’re right they’re more accountable than QG guys, but not much more. I am much more of a partisan of astronomers. Evolutionary biology often flirts with being non falsifiable piffle, though of course we all know it’s right in the broad strokes. Stuff like evolutionary psychology, or even, god help us, evolutionary literary criticism: almost total baloney. Dawkins is hilarious: for all his self regard, his sociobiological determinism will very likely read like a book of medieval demonology in 200 years.

          I think you’re misunderstanding me on the career thing. I’m not saying it’s easier to be a professional quantum gravity auteur than a condensed matter physicist or any other kind of physicist. You’re right: QG sucks as a career path. I’m just saying there is no real way to be an authentic original thinker in physics. Let’s say I want to study something super important and original, like, say, why life is chiral. Maybe it’s just an accident life is chiral, but it is something most reasonable people would agree is important to know about. It is also something barely studied at all. Because it is barely studied, and because of the nature of how science gets funded, there are no professorial chairs available for this problem at all. Hell, I’d be surprised if there were any post-doc positions available doing this sort of theoretical work. By contrast, there are hundreds of positions available to string theorists, and maybe a half dozen for loop quantum gravity dudes who have some cosmological hobbies as well. Dr. Chirality is well and truly hosed. If he’s lucky, he’ll get a job on Wall Street, and a cruel bastard like me will keep him employed thinking about less important things. What good is a university if it’s just perpetuating a sort of intellectual pyramid scheme in this way? Burn ’em down!

          I think there are all kinds of things like chirality and the things I talk about above which can and should be studied. They ain’t, because you’re all off trying to make grand predictions like late Einstein, rather than doing the awesome small “understanding shit” physics of early Einstein. Let’s face it: early Einstein was great, but late Einstein was like fat Elvis.

  7. Nav said, on October 16, 2009 at 8:23 pm

    I’d be wary of claiming nothing good has come out of unification physics. The big innovations in mathematical/theoretical techniques in physics have, to a large part, originated in high energy physics. And those techniques lie at the heart of our modern understanding of soft and hard condensed matter (polymers, glasses, superconductors electronic devices etc.), along with shaping our comprehension of phase transitions (possibly the single greatest achievement in theoretical physics in the late 20th century was Wilson’s use of the renormalisation group to explain critical exponents in phase transitions). I think you’re undervaluing the ancillary benefits of esoteric research – it might be useless in and of itself, but it tends to produce an awful lot of tangentially useful stuff.

    As for chairs in chirality… Well, first off people do study this, most specifically in the context of the dreaded unification and the existence of chiral fermions in various different UV completions of the Standard Model. Also, you can’t have chairs or postdocs in nominally interesting stuff, if for no other reason than you don’t know, a priori, what that stuff is. Rather, the best you can do is hire smart people and see where there interests take them. And you see this with string theorists, these days a lot of people wander off the unification reservation to work on other problems where strings come in handy (condensed matter is all the rage at the moment). Great physicists don’t tend to constrain themselves to some tiny little subfield, they devote themselves to whatever happens to be most interesting to them at any given moment.

    • Scott Locklin said, on October 16, 2009 at 8:47 pm

      OK, I’ll grant you that some cool math with useful benefits to other fields has come out of some of high energy physics. Certainly the last several decades of high energy physics were good for math. And I agree that Wilson’s Nobel was an awesome achievement. But my point remains: why not think about, say, statistical physics at the rate we do on quantum gravity? Maybe some math which is directly useful for statistical physics will come out of studying statistical physics, rather than hoping high energy peregrinations will help.

      I know about weak field chirality being suspected as a possible reason life is chiral, but I’m unaware that there are lots of serious people thinking about it at the types of energies involved in forming sugar molecules. Thus far, it remains a big fat mystery. One you’re confronted with every day when you put sugar on your cheerios. Anyway, it’s just a dumb example of an important problem that requires no machinery the size of the universe to solve: there are lots of interesting things people could be thinking about in great numbers but ain’t. I don’t know how to fund original thinkers in university systems. Maybe we should give more physicists jobs in the patent office, or drilling holes in cannons?

      Anyway, before we each get out our numchucks: I got to go do some work. I don’t get paid to think about physics -and it probably shows!

      • Nav said, on October 16, 2009 at 8:59 pm

        Fair enough on the direct study, that’s been bothering me for a while. As for jobs in patent offices, well I’ll take anything that’ll keep me employed!

        It’s been fun, and while I do get paid to think about physics, I don’t think blog comments were quite what the University of Texas was imagining when they hired me… Thanks for the stimulating exchange.

  8. […] October 17, 2009 Today, I was inspired by a post of Dr. Scott Locklin, which can be found here. […]

  9. Driveby said, on October 22, 2009 at 4:09 pm

    “Science is about learning about how the universe works, not seeking aesthetic answers to questions that the universe isn’t asking.”

    …and yet, there’s Democritus, with his picture in all the Chemsitry textbooks…

    • Scott Locklin said, on October 22, 2009 at 7:55 pm

      And … how many philosophers got it wrong? Selection bias is a sin.

  10. Arthur said, on October 27, 2009 at 2:27 am

    What aspects of the 2nd Law are still unexplained? I guess I am satisfied by the explanation that it’s simply a matter of probability. If you have a high pressure of gas on one side and a low pressure of gas on another side of a barrier, the fact that they will mix together upon removing the barrier is akin to flipping a coin 2 million times and producing about 1 million “heads” and 1 million “tails.”

  11. Charles Kinsley said, on February 27, 2010 at 4:47 pm

    OK, I just stumbled across your website from a search of “I hate Lee Smolin” engendered from a talk I attended last night given by Amanda Peet (String Theorist) in Toronto. I was schooled in theoretical physics but have never worked in the field, but I was astounded at the displays of venom I witnessed when the names Smolin and Anderson were raised. My personal historical inspiration for studying physics was the period from 1647 – 1960. I now realize this was an exceptional and fruitful period. Perhaps the normal model for science is this stumbling around that we tend to see at present, because science does not proceed logically. Creation is a series of irrational stabs at things – very few of which turn out to have any separate, significant meaning.

    • Scott Locklin said, on February 27, 2010 at 8:48 pm

      Well, I certainly don’t hate Lee Smolin, I just think he doesn’t go far enough. I’m sure the reason some people do is he and Anderson (among others) are laughing at the pretensions of the 10,000 or so String-a-dings out there counting angels on the heads of pins.

      Saying 1647-1960 was an exceptional period, well, that seems wrong to me somehow. I think it’s more accurate to say that intellectual discourse since 1970 or so has been in a steep decline, rather like everything else in Western Civilization; art, literature, poetry, architecture, aeronautics, space flight, education, even software engineering.

  12. cfmceroz said, on May 27, 2010 at 6:08 pm

    I enjoy Lee Smolin’s books, but this article is a great counterpoint. and hilarious as well! I would like to read more on the important topic of autodidactic research in the internet age

  13. […] breakthroughs, in scientific education these sort of leaps are presented as normal. This causes enormous problems in the scientific community, as you get lots of people who aren’t really doing science any […]

  14. Yonemoto said, on October 4, 2010 at 9:22 am

    I’ll have to counter with beef about your five problems. One of them is good. The other four are utter crap.

    The fundamentals of quantum mechanics. This one is good. Perhaps, not surprising. Because it has survived both Smolin and you.

    The second law of thermodynamics, chaos and the arrow of time.
    A very important question. But you have largely veered out of the domain of theoretical physics and into practical physics. We’ll need a lot more data points to figure this one out (i’m guessing the big big big question is has unversal entropy stayed the same over time). Much of the work in local effects of 2LT has been hashed out by chemists and biophysicists (an awful moniker for what is basically a chemist); so naturally it’s left the area of concern of physics.

    Self-organization and emergent properties in matter.
    Squarely in the domain of chemistry. Largely speaking, chemistry is the study of matter (its diversity and interactions with energy) versus physics which is the study of energy and its interactions with matter. Physicists have no business doing their work in these fields. Once a physicist embarassingly wrote an excited blog post about detecting self-organizing patterns in an AFM image of a self-assembling protein. A chemist took one look at the AFM image and told the physicist it was a salt crystal. This isn’t an attempt to ‘carve out’ turf in the scientific scheme; rather it’s just a pointed opinion that by the time a physicist has enough experiential knowledge to truly contribute to something in that field, they ought to be calling what they do chemistry. Just as a chemist that has enough experiential knowledge to truly contribute to, say string theory, ought not to label those efforts as chemistry. I’m not going to entertain the counter that labels don’t matter, because I could just as easily say top five lists don’t matter.

    Why is life? Never mind “how does life work,” tell me why life works at all!
    This has largely been worked out by biology, biochemistry, and a few patches are being put on by biophysics (like the forces of how DNA unwinds and muscles contract). There really are no more questions about, say, mass balance, or energy balance. the big picture of what structural organization events occur (like mitosis) are solved by brute microscopic observation – and what remains are details of what genes and chemical mechanisms are associated with getting those rearrangements to occur. A handful of truly physics problems exist (magnetoception) but it seems like the biochemists, by virtue of a few people who understand the physics behind the wonderful instrumentation that physicts and materials chemists have bestowed upon them – seem to be chipping away at figuring it out. The biggest remaining fundamental life science problem, as I see it, is to figure out what chemical reactions are necessary to bootstrap life, and what the statistical probabilities of those occurring are in the early soup.

    How do neural computers, aka brains work?
    You don’t honestly think that the biochemists, cell biologists, and neuroscientists are chipping away at this problem? Physicists are notoriously bad at figuring out problems of emergent nature (although with new condensed phase studies into things like non-newtonian fluids that may change). It’s not clear to me that physics is the correct discipline to address this. If anything, good top-down models (seriously lacking) will come from the computer scientists.

    It surprises me, conversely that there so, so many distinctly non-fundamental questions in physics which are easy to state and quite easy to observe but difficult to explain. Call them the physics equivalents of the ‘hailstone problem’.

    Granular convection, for example. Or this one. http://www.newscientist.com/article/mg18624935.200

    • Scott Locklin said, on October 4, 2010 at 2:35 pm

      I think self organization is pervasive enough a phenomenon, we can’t just leave it to the chemists, even if some physicists get silly about this on occasion. I mean, the physicists did figure out how phase transitions and things like magnetism work; as such, I expect it will be physicists who figure out how other kinds of self organization work. Really, I count Progogine as a physicist, despite his unfortunate background. I’d also say a lot of such problems remain in the “what is life” question, though it may be my towering ignorance in this subject which causes me to say so.

      Neuroscientists have made some progress … they know all about, for example, eyeballs and stuff, but they still haven’t a whit of a clue as to how a brain works. Not even the beginning of a beginning understanding. Sea slug brains made of only a couple of neurons remain mysterious. The way they are chipping away, is, as you say, kind of reductionist: and so it might never bear any fruit.

      I’m with you on the various non-trivial problems not explainable by physics. Flying Circus of Physics is a great book which talks about some such problems.

      Of course the second law is something we should be able to understand with theoretical physics. It’s not practical in that the practical consequences are kind of understood already: I consider it deeply philosophical. Much deeper than noodle theory.


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