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 example than that used in 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?
**1. Quantum mechanics might allow instantaneous communication across any distance!