Where Good Ideas Come From

The Natural History of Innovation

by Steven Berlin Johnson

Go to the Reef, Thou Dullard, and Consider Its Ways

I looked forward to this; Johnson's Emergence is still one of two books that I point people to explain what I do, or used to do (the other one being my former boss Melanie Mitchell), and I think he's one of our best — most astute and wide-ranging — popular writers about science and social science, which means he almost has my dream-job of being a science critic. And I mostly got what I expected. This is 100-proof American evolutionist, naturalistic liberalism, which is to say, Pragmatism. It is a celebration of the virtues of openness, experimentation (including failed experiments), giving "slow hunches" chances to develop, to serendipitously blending ideas from diverse intellectual backgrounds and disciplines, and the continuity of human culture and thought with processes in the natural world. It's a view of the social life of the mind, illustrated by engagingly-told anecdotes from the history of science and technology; apt references to a wide range of scholarly studies; long, admiring quotations from Darwin; the natural history of coral reefs and the evolution of sexual reproduction. (The broader history of culture, especially the fine arts, is occasionally alluded to, and there are abundantly merited plugs for his old teacher Franco Moretti's studies on the evolution of genres and "distant reading"; but mostly it's a science-and-technology book.) Johnson has painted a crowd scene: good ideas hardly ever come from isolated individuals thinking very hard and having flashes of inspiration; they come from people who are immersed in communities of inquiry, and especially from those who bridge multiple communities. The picture is an attractive one, which I actually think (or perhaps "fervently pray") has a lot of truth to it. But I feel like being contrary, while I do not feel energetic enough to arrange my objections, reservations and extensions as a coherent argument, rather than a series of numbered points.

1. While "good ideas" are there in the title, and the phrase is repeated often, Johnson never comes to grips with what makes some ideas good; at most he gets at complex, successful and influential. (This is common problem with Pragmatism.) The formation of fascist ideology, before it seized power, is a story of loose, open networks of thinkers bringing together a very diverse set of eminently-respectable traditions into new and unexpected configurations, nurturing long hunches, meeting in coffee-houses, etc., etc. The kind of social processes which gave us fascism were not that different from the ones which earlier gave us democratic ideology, but one set of ideas was very good and the other very bad, though exquisitely adapted to its setting. At an immensely lower level of wrongness and harm, psychoanalysis has proved scientifically and therapeutically fruitless, but fits Johnson's ideas so well that he alludes to it several times. Perhaps one could say that by focusing on science and technology, where there are much clearer (though still not entirely clear!) criteria for "good", Johnson largely evades this.
2. You can't have interdisciplinary breakthroughs without first developing disciplines, and that to a very high level; but Johnson systematically neglects how innovation happens other than through cross-fertilization. (The imaginary Johnson in my head retorts that opening up a single discipline would reveal a cluster of sub-disciplines, and so forth, and it's cross-fertilization all the way down. Perhaps.) We've had this discussion before, many times: a lot of very narrow, technical, incremental work has to go in to creating the sophisticated, precise, accurate, powerful ideas that can be productively recombined. I find such work less congenial than the recombination, but if the interdisciplinary ideas are any good, pursuing them will lead to a new discipline, if things go well.
3. Johnson writes as though he doesn't appreciate the trade-offs between different kinds of errors, and the reasons why their costs might vary with circumstances. (I am pretty sure I he has written about the trade-off elsewhere.) This matters, because the trade-off forms the core of a case for stubborn conservatism and refusal to speculate. (What follows is Burke re-done in the language of "sophists, economists and calculators" — that is, of the Neyman-Pearson lemma.)

   As Johnson says here several times, most ideas are just foolish. Accordingly, we have a lot of opportunities to mistake them for good ones ("false positives"); and of course we could think what's actually a good idea is a bad one ("false negatives"). Reducing the false negative rate, by cultivating more unlikely-seeming hunches, pursuing far-reaching connections, etc., is, beyond a point, only going to happen by increasing the false positive rate.

   One of Johnson's examples is contrasting the speed, flexibility and experimentation of Web software development with the sheer stodginess of the FBI, and in particular how it failed to bring together two lines of intelligence that, in hindsight, pointed to the 9/11 plot. Now, that was — and I realize this is putting it very coolly — certainly a false-negative error. But Johnson gives me little reason to believe that there was any way of getting the organization to act on those hunches without also acting on many other hunches which were, even in retrospect, just no good. How many speculative memos like "the Phoenix Memo" were written in the FBI in the summer of 2001, which proved to be dead ends? How much work would pursuing each one have called for?

   As a society, we have decided, at least when we're at our civics-class best, that false positives on the part of the police are so very bad that we will tolerate quite a lot of errors the other way to avoid them. This is, to review, because (1) we want to be safe from the police, and those who run the police, (2) we dislike unleashing the snooping, harassing, arresting power of the state on innocents, and (3) while the police are chasing phantoms, they are not dealing with actual criminals. In contrast, the worst that happens when a silly Web startup is funded is that a few million dollars get frittered away in the Bay Area and/or lower Manhattan, and as someone who likes geeks in both places I can't see even that as a total loss. (Remember, Johnson was the one who brought up the comparison, not me.) It is a good thing, then, that the Web is much more tolerant of false positives than is the FBI. (The latter's antiquated IT system is another matter.) I am not asserting that the FBI is up against its error frontier, and could only reduce false negatives by making more positive errors — how would I know? — but I am pretty sure that if it acted on speculation as readily as the Web development community, it would be a danger to the republic and would need to be shut down.

   This point, about trade-offs between different kinds of errors, is arguably related to the previous one about disciplines.* The false-positive/false-negative dilemma is going to face any institution which needs to come up with ideas and judge them, and it might help us to understand and reform those institutions by thinking about this consciously. The disciplines aim at increasingly precise, accurate and elaborate understandings of fairly circumscribed domains. With goals like that, false positives need to be suppressed; "single vision, and Newton's sleep" is the way to see deeply. Of course even the most focused discipline has a frontier where it is figuring out new things, and so it is not clear in which direction one should go. There, among those mapping the frontier, the discussion needs much more tolerance for false positives than does teaching, or sharing work with other disciplines, or actions which up-end people's lives. Parts of the apparatus of scholarly communication can be rationalized as applying successive filters with more and more tolerance for false negatives, but it's hard to believe that this couldn't be much improved upon, or that the counterparts in any other domain are any closer to optimal. The rational kernel of what Johnson is saying is, perhaps, that many organizations would do well to cultivate some mechanism for encouraging ideas, even with a lot of false positives, and then filtering then once they've had a chance to grow.

4. In the final chapter he straightforwardly admits that no matter how many wonderful anecdotes he piles up of collaborative, openly-shared innovation, an opponent could come up with many other anecdotes of secretive, isolated innovators driven purely by the prospect of reaping monopoly rents (i.e., returns on intellectual property). Something more systematic and synoptic is needed, he correctly says, and proceeds to give it, inspired by Moretti's "distant reading" of the genres of English novels. He pulls together a list of several hundred major scientific and technological innovations since about 1400 (it's in an appendix), and classifies them all as either market-driven or not, and either the products of individuals (including single firms) or networks. He observes that remarkably few of them fall in the market-driven, individual box, and remarkably many — increasingly many — in the non-market, networked box.

   Here's where I really show the depths of my ingratitude: Johnson is completely right to do this, and it puts him far ahead of almost any other comparable writer, but I am still not satisfied. Where did he get candidate innovations for his list from? How did he decide whether something was major enough to belong? How did he individuate innovations? (Saying that E = mc² and the special theory of relativity are two separate innovations seems odd to the physicist in me.) For that matter, there is another way of looking, systematically, at the kind of question Johnson wants to answer here, which is statistical inquiry, in this case econometrics. It's been known since the 1990s, at least, that it's hard to show any positive influence of strengthening, or creating, intellectual property rights on innovation. For that matter, just in the last month two papers have crossed my virtual desk, showing that there is if anything a negative relationship, at least for genomic medicine and software (both via Kevin Bryan's A Fine Theorem blog [1, 2]). It would be deadly, in a popular work like this, to go over the analyses, but I don't think it's unreasonable to expect Johnson to have gone looking for this sort of social science, and to relate its findings to his readers.

5. The last chapter also, naturally, raises the question of what public policy towards innovation should be like, and in particular whether innovation is best encouraged by the coercive power of the state creating and enforcing monopolistic market inefficiencies, i.e., intellectual property rights. About this, Johnson is rightly skeptical, and I have to give him a lot of credit for both raising the issue and for taking the stand he does, since it cannot possibly help his sales prospects. But he does not go very far into this, and he spends a lot of time and rhetorical effort reassuring the reader that he is not a commie. (He repeats the myth that Marx offered to dedicate Capital to Darwin, a legend that should have died more than thirty years ago.) But I don't think he does an adequate job of explaining why someone who buys his arguments should not, in fact, be at least a bit of a commie (especially a bit of a Kropotkinite anarcho-communist**), and the broader discussion of what we should do with his ideas is a bit superficial. To be fair, it's a huge area, I doubt anyone has really good conclusions yet, and no matter what one writes it is unlikely to win friends, so perhaps saying "just think about it, OK?" is the most that could be expected. — I wrote this paragraph before seeing Henry Farrell's related post, so you should probably go read that.
6. As may have become evident, Johnson's boosterism of the Web (and even of specific companies) grows tiresome to me. I say that as someone who's been enthusiastic about the Web since 1994, and whose life and career would have been very different (and probably worse) without it.

Some of my carping above is probably just from my own reading having obviously overlapped too much with Johnson's, so that I am close enough to see flaws and infelicities, but not to appreciate how it would look to someone coming to it for the first time. This is not as good a book as I was hoping for, but it's still a good one, and with any luck it will noticeably raise the level of public discussion.

*: I owe the thought which follows to a conversation at SciFoo 2010 with Jen Dodd and Michael Nielsen, and possibly (there were some beers involved) Eric Drexler. Credit for any insight goes to them, blame for folly is all mine.

**: I will repeat a quotation from Bertrand Russell (Proposed Roads to Freedom: Socialism, Anarchism and Syndicalism, ch. V, his italics but omitting footnotes).

Kropotkin ... points out how much has been achieved already by the method of free agreement. He does not wish to abolish government in the sense of collective decisions: what he does wish to abolish is the system by which a decision is enforced upon those who oppose it. The whole system of representative government and majority rule is to him a bad thing. He points to such instances as the agreements among the different railway systems of the Continent for the running of through expresses and for co-operation generally. He points out that in such cases the different companies or authorities concerned each appoint a delegate, and that the delegates suggest a basis of agreement, which has to be subsequently ratified by each of the bodies appointing them. The assembly of delegates has no coercive power whatever, and a majority can do nothing against a recalcitrant minority. Yet this has not prevented the conclusion of very elaborate systems of agreements. By such methods, so Anarchists contend, the useful functions of government can be carried out without any coercion. They maintain that the usefulness of agreement is so patent as to make co-operation certain if once the predatory motives associated with the present system of private property were removed.

History of Science; Philosophy of Science; Popular Science

Currently in print as a hardback, ISBN 978-1-59448-771-2, US$26.95