Book review: How the Hippies Saved Physics

Yes, it’s another of my patented non-timely book reviews. At the long-ago suggestion of frequent commenter Jeff Ollerton Artem Kaznatcheev, I just read David Kaiser’s How the Hippies Saved Physics. Here’s my review, which as usual is less about the book and more hopefully-interesting thoughts inspired by the book.

Yes, I know this is useful to like minus-seven of you. Whatever. If all our posts were useful, you’d forget how useful the useful ones are. You’d get tired of winning reading useful posts.*🙂

tl;dr: It’s a fun and thought provoking book, you should totally read it. Click through if you care why I say that, or if you want to read my half-baked thoughts on the non-tradeoff between creativity and rigor in science, the challenges of pursuing theory-free research programs, and whether there’s really such a thing as a “productive mistake”.

The book centers on the Fundamental Fysiks Group, a free-ranging discussion group organized by some young PhD physicists at the Lawrence Berkeley national laboratory in the early 1970s. Group members shared interests in the interpretation of quantum mechanics, particularly quantum entanglement and Bell’s “no hidden variables” theorem. They were also really into purported links between quantum entanglement and New Age subjects like ESP, telepathy, and Eastern mysticism. Kaiser argues that group members “saved” physics in the sense of importantly influencing its direction via unconventional routes. Those routes organizing conferences sponsored by eccentric millionaires, circulating preprints, and inventing a new genre of popular science book (The Tao of Physics is by Group member Fritjof Capra). Group members had to pursue their interests (and in some cases support themselves) via unconventional routes because conventional ones were closed to them. Academic physics was undergoing a major contraction associated with decreased funding, and mainstream physics journals weren’t interested in what was seen as idle philosophical speculation. Kaiser uses the example of the Fundamental Fysiks Group to draw two larger lessons: that there’s no clear-cut distinction between “real” science and “fringe” science, and that modern science overvalues technically-correct solutions to small questions over creative (and so necessarily error-prone) speculation about big questions.

The book has many strong points. The author has a PhD in physics, and it shows; he’s an excellent explainer of highly technical material. He picked a great example to make the case that there’s no clear bright line between science and non-science. It’s a much better than Michael Gordin’s The Pseudoscience Wars, which concerned a much fringier group of people who had no lasting influence. But don’t worry–Kaiser’s no postmodern relativist. He’s completely clear that the Fundamental Fysiks Group got a lot of things wrong, but argues that their errors were productive. Group members asked good questions, and the efforts of others to refute their errors led to an important fundamental insight with practical applications: quantum cryptography. The chapters on how Group members pioneered new ways of communicating physics were a highlight for me. And like any good popular history book, it’s an entertaining window into a specific time and place–here, the Bay area in the 70’s. And it’s packed with interesting characters. “Characters” being exactly the right word for many of them…The book is both full of ideas and a page-turner, which is a great combination. And if the title of the book ends up seeming like an overstatement, well, as a blogger I’d never blame anyone for indulging in a deliberately provocative title.🙂

Among other things, the book illustrates the difficulty of pursuing a purely empirical, theory-free research program, especially when you really want it to reach a particular conclusion. Probably most scientific readers will find themselves wincing repeatedly as they read about the Fundamental Fysiks Group’s Underpants Gnome Theory of Parapsychology**, how easily group members were fooled by Uri Geller, and how swift they were to seize on statistical noise in badly-designed, underpowered ESP experiments. Kaiser doesn’t think that stuff was good science, but he implies that it went hand in hand with doing good science. That if you’re being creative and asking big fundamental questions, well, sometimes you’ll end up trying to use quantum typewriters to communicate with the dead. I’m not so sure. After all, various other people mentioned in the book shared at least some of the Fundamental Fysiks Group’s interests in non-mainstream topics like Bell’s theorem–but didn’t share the Group’s interests in parapsychology. Or think of George Price, another fringe-y figure, but one who combined big ideas and great scientific creativity with a hard-headed skepticism about parapsychology. And conversely, Andrew Gelman would probably argue that lots of psychologists today make the same sort of mistakes as Fundamental Fysiks Group members did in their ESP work not out of an excess of creativity but if anything out of lack of creativity–wanting to routinize scientific discovery and continuously churn out “breakthroughs”. Anyway, I found myself thinking more about successful theory-free or theory-lite research programs vs. unsuccessful ones. One thing I’m wondering is if having a weak or sketchy theory is actually worse than having no theory at all. Or maybe the issue is that it’s very hard to improve a sketchy theory by trying to “test” it experimentally. I’m also thinking more about whether there’s necessarily a trade-off between creativity and rigor in science. Seems to me that one could combine a willingness to try crazy experiments like ESP experiments with an ability to design them well and a willingness to give up on them quickly when they don’t pan out.

It’s not a perfect book. It’s organized topically rather than chronologically: there’s a chapter focusing on Group members’ interests in parapsychology, a chapter on how they circulated their ideas, etc. That was probably the best choice on balance, but it inevitably makes sequences of events tough to follow. Maybe I wasn’t paying sufficient attention to dates, but I didn’t realize until most of the way through the book that a decent number of the events described actually predated the first meeting of the Fundamental Fysiks Group in 1974. More importantly, as another review notes, one can seriously question Kaiser’s claim that mainstream physics in the 1960s and ’70s wasn’t making fundamental progress. It was during this time that the Standard Model fell into place. And if mainstream physicists of the time weren’t asking philosophical questions about the interpretation of quantum mechanics, well, maybe that’s because those questions couldn’t possibly be answered with the technology available at the time. As Kaiser emphasizes, the previous generation of physics giants–Einstein, Bohr, Heisenberg, et al.–also asked philosophical questions. But as Kaiser doesn’t emphasize, those questions led to good experiments. It’s telling that one of the most lasting influences of the Fundamental Fysiks Group was the one really good physics experiment any of them was involved in–the first test of Bell’s theorem. As we’ve discussed before, you can’t influence the direction of a scientific field solely via conceptual speculation, and there are good reasons for that.

In passing, it’s interesting to compare this book to Lee Smolin’s Not Even Wrong. Smolin complains that string theorists today are the sort of unphilosophical, shut-up-and-calculate types who are the villains of Kaiser’s book. But Smolin also complains that string theory is unscientific because it’s totally disconnected from any possible experiment. Another bit of evidence that there’s no necessary trade-off between creative speculation and empirical rigor in science.

A big issue I’m still mulling over: what exactly does it mean to say that a scientist has “asked a good question” or “set the direction for the field”? Here, if someone makes a scientific mistake that can be refuted based on what we already know, and others eventually build on the refutation and develop a productive new line of research on a different topic, how much if any credit should go to the person who made the original mistake for “asking a good question” or “setting the direction for the field”? Shouldn’t credit go to the person who refuted the mistake, or the people who realized the implications of the refutation? And even if not, does being influential somehow compensate for being wrong?

*At least, that’s what I tell myself every time Brian or Meg posts something useful, which is pretty much every time they post.

**1. Quantum mechanics might allow instantaneous communication across any distance!

2. ???

3. ESP!

10 thoughts on “Book review: How the Hippies Saved Physics

  1. “Smolin also complains that string theory is unscientific because it’s totally disconnected from any possible experiment. Wow! So a scientist to believing in string theory is like a christian believing in creationism? That’s a splash of cold water (aka humility) worth thinking about.

    • I wouldn’t put it that way and I don’t think Smolin would either. Creationists have a predefined conclusion they want to draw. As Smolin tells it, string theorists are just over-valuing certain desirable features of good theory while under-valuing current testability.

  2. My kind of book review and sounds like my kind of book, Jeremy! (and I have The Tao of Physics on my shelf, but haven’t yet got up the courage to read it.)

    Yes, I think the person who asked the question, even though wrong, advances the ball. You know how Edison said he figured out 2,000 ways not to make a light bulb? Well, if he would have quit on 1,999 someone else would have gotten the credit and he would have been forgotten because society only likes winners. Yet everything society has was built not only on the successes but the failures of our ancestors so I think it’s short-sighted to only like the winners. Everyone contributes something and since we’re all part of the morphogenic field, both the successes and failures are being telegraphed telepathically to whoever is listening — consciously or not — and hopefully helping us evolve (or perhaps implode if American elections are any example) as a species.

    And lest you think your words and “half-baked thoughts” aren’t getting out there to more than “minus-seven” of us, they, like everyone else’s thoughts, and like the truth, to quote The X-Files, are out there mixing in with all the other half-baked thoughts creating our reality. So make them good thoughts and keep writing these great book reviews!

  3. One of us has clearly been smoking too much Hippie Herb, Jeremy, because either I’ve forgotten that I’ve ever read this book, or you’ve misremembered who recommended it. I’m going to vote for the latter🙂 Sounds great though.

  4. Good one Jeremy, I’m definitely among the negative seven here. And I’m pretty much entirely with your position.

    “…Kaiser doesn’t think that stuff was good science, but he implies that it went hand in hand with doing good science. That if you’re being creative and asking big fundamental questions, well, sometimes you’ll end up trying to use quantum typewriters to communicate with the dead. I’m not so sure.”

    Fully agree and would go further and say “Sorry, that argument doesn’t hold water”.

    I don’t think there’s any question that scientists as a group should not fall entirely into strictly rote behavior patterns dominated by unimaginative thinking, even though a lot of that is in fact required to get the overall job of science done–a lot of mundane stuff has to be done. But It’s one thing to be creative and expansive, and another thing altogether to be irresponsible and attention seeking in the process, which IMO sometimes (often?) motivates various claimed attempts to “advance the science”. I have seen, among certain groups of scientists, behavior which goes along the lines of: “Ha Ha, look at that crackpot, Uri Geller, claiming to bend spoons by telepathy, what a non-scientific ruse–this is exactly why science is better/useful, we would not make such dumb mistakes, science is the guard against just such claims”, etc.

    But then these same folks will publish a paper in which they base their conclusions on one or more flaws, which might include things such as poor base data sets, poor statistical analysis, poor logical inferences, and the ever-popular wild over-generalization, or at best, poor descriptions/documentations of what was actually done, such that the merits cannot be well judged. This type of thing of course happens in science, but when criticized on their basis I have seen these folks jump immediately to this basic argument in defense, though stated in various ways–“We have posited a plausible result (the first to do so we might add!)…science advances due to that creative few who take risks..we are not to be blamed for the limited observational data available…science involves paradigm shifts and somebody has to start that process…”, and similar kinds of arguments. Sure, I guess, whatever…Kuhn would like it. Except for the fact that you don’t really have a strong argument, due to various weaknesses in how you got to it. In no way do I buy the argument of “Well we deserve credit for expanding the though envelope on this topic, further testing is welcome, blah blah whatever”. Anybody can come up with imaginative ideas–look at how many fiction writers there are in the world. If I want to read “plausible, but evidence challenged” I’ll read some of that stuff.

    • If you haven’t seen it, you’d like Andrew Gelman on the “scientific surprise two step”. It’s when you draw a surprising conclusion from scanty evidence, but when the plausibility of the conclusion or the scanty evidence is challenged, you respond that the conclusion is actually very plausible, just what theory predicts, etc.

  5. Hi Jeremy; I have not read the book, and probably would not based on your description ; Any book on the history of physics that claims the 60s and 70s were not a time of revolution in physics[ mainstream at that], particularly particle physics , is quite suspect.
    There are several nice, readable, histories on the 20th century in particle physics. My 2 favorites are the quite technical INWARD BOUND, by Abraham Pais ,and THE SECOND CREATION, by Robert Crease and Charles Mann [ 2nd edition, 1995]. The C&M book has the subtitle of ” makers of the revolution in twentieth-century physics’ , is great , quite readable for scientists in general, and based partly on interviews with many of the modern players in particle physics; I have read it maybe 5 times. Its about the process of discovery[ machines , experiments, people( many very colorful) & ideas] as well as the discoveries themselves. It ends with a description of String Theory, …attitudes , criticism ( much), possibilities, etc, ca 1995. Its well worth reading for how fundamental science gets done.
    If one searches with google for the 2 names together…. Geoff West [ a main player in Metabolic Theory of Ecology: aka west, brown, enquist] and Murray Gell Mann , one of the first hits is a few hours of interviews by Geoff of Murray, an autobiographical version of the creation of the Standard model of Particle physics. Murray is, of course, one of the major contributors to (particle) physics in the period 1950-1980. well worth listening to.

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