The transfer method

A few weeks ago, I picked up a worn paperback copy of The Art of Scientific Investigation by W.I.B. Beveridge, which I expect will join the short list of books on creativity that I’ll never get tired of reading. It was first published in 1950, but it’s still in print, and it isn’t hard to understand why. Beveridge’s book is essentially a collection of recipes or approaches for coming up with ideas, with meaty chapters devoted to the roles of reason, intuition, chance, and imagination, and it’s loaded with concrete, practical advice. Take the section on what Beveridge calls the transfer method:

Sometimes the central idea on which an investigation hinges is provided by the application or transfer of a new principle or technique which has been discovered in another field. The method of making advances in this way will be referred to as the “transfer” method in research. This is probably the most fruitful and the easiest method in research, and the one most employed in applied research. It is, however, not to be in any way despised. Scientific advances are so hard to achieve that every useful stratagem must be used.

The italics are mine. Success or failure in resolving any problem often boils down to a knowledge of the available tools, and this often requires familiarity with advances in apparently unrelated fields. One of my favorite recent examples comes from the field of adaptive optics. When astronomers are viewing an object through the earth’s atmosphere, which distorts light, they’ll shine a laser in the same direction. When the light from this artificial “guide star” returns, they can measure the distortion, then use that data to adjust their telescope to cancel out the aberrations, which gives them a much more accurate view of the object under observation. The physicist Eric Betzig took the idea of a guide star and applied it to microscopy, which also has to deal with optical information being warped by an intervening medium, which in this case is organic tissue. Taking a cue from astronomy, the technique creates a guide star by focusing light from the microscope on a fluorescent object in the sample, like an embedded bead. After using a wavefront sensor to determine how the light was warped, it can make the appropriate corrections. And because tissue causes more complex distortions than the atmosphere does, it employs yet another strategy—derived from ophthalmology, which uses it to correct images of a patient’s retina—to average out the error. The result won Betzig a Nobel Prize.

And it isn’t hard to see why Betzig paid close attention to astronomy and ophthalmology. These fields may study different classes of objects, but they’re all ultimately about dealing with properties of light as it passes from the observed to the observer, which has clear implications for microscopy. Betzig and his collaborators were shrewd enough to frame their work in the most general possible terms: it wasn’t about microscopes, but about light, and everything that dealt with similar problems was potentially interesting. Being able to correctly define your field—which has more to do with the concrete problems you’re addressing than with labels imposed from the outside—is the first step in identifying useful combinations. And even trained scientists have trouble doing this. As Beveridge notes:

It might be thought that as soon as a discovery is announced, all its possible applications in other fields follow almost immediately and automatically, but this is seldom so. Scientists sometimes fail to realize the significance which a new discovery in another field may have for their own work, or if they do realize it they may not succeed in discovering the necessary modifications.

Of course, it isn’t possible to read or absorb everything, so you need to be smart about how you filter the universe of available material, which can be done from either end. You can start with a solution and then look for interesting problems: Beveridge cites several examples of techniques, such as partition chromatography, in which researchers systematically cast about for fields in which it could be put to use. Alternatively, you can keep a handful of problems perpetually before you, and use it as a kind of sieve to isolate useful ideas, as Gian-Carlo Rota describes:

Richard Feynman was fond of giving the following advice on how to be a genius. You have to keep a dozen of your favorite problems constantly present in your mind, although by and large they will lay in a dormant state. Every time you hear or read a new trick or a new result, test it against each of your twelve problems to see whether it helps. Every once in a while there will be a hit, and people will say: “How did he do it? He must be a genius!”

This is essentially what novelists do. When you have the basic premise of a story in mind, suddenly everything you see becomes relevant—which is a good argument for coming up with at least a general outline as early as possible. But you don’t need to be a novelist, or a scientist, to find a guide star of your own.