On The Tacit Process of (Scientific) Discovery
In a recent coffee break, a discussion broke out about the naming of things in science. For instance, you have the Boltzman constant, Shannon entropy and the Golgi appartus. Then there are the bizarro names given to classic thought experiments such as Maxwell's demon, the Einstein-Podolsky-Rosen paradox and Schrodinger's cat.
Someone remarked that people don't seem to name things anymore. Except that they still do. In my field, I can think of some recent namings such as the Karplus coupling, the Levinthal paradox, the Ramachandran plot and the Connolly surface. Coining new names is easy, and one might be tempted to think that new names just adds to the cess-pool of new jargon, which is very deep indeed. But the use of jargon is not necessarily bad. It's just that so very names actually pass into useful common usage. This only happens if the new name encapsulates a complicated idea, and the idea is useful, and the new term pops, then communication amongst professionals is enhanced.
Still the coining of names brings up an interesting question: why do we decide that a person shall be forever conjoined with an idea? Naming a idea after a person is perhaps the highest honor we can give to a fellow scientist for discovering that idea in the first place. It suggests not only that the scientist did in fact discover it, but the discovery is one of consequence.
Still the debate over who discovered what, may seem like an armchair debate, but there are often major consequences. Like any kind of competition, there are no prizes for coming second. Publication of a new experiment often prevents the publication of similar experiments coming after. And grants and research money flow through the doorway of a good publication record.
Life-long shit fights have been fought over the originality of scientific ideas. The classic example is Isaac Newton and Gottfried Leibniz fighting over the mantle of the inventor of calculus. Newton was known to have made up pseudonyms to pen articles attacking Leibniz in various scientific journals. In that particular butting of heads, the entire scientific communities of Germany and England were enlisted to fling shit at the other side over a period of decades.
The problem with the attribution of originality is that discovery can be plausibly broken into 4 different persons. There is 1) the person who brainstormed the initial idea, 2) the person who got a working prototype of the idea, and 3) the person who got the prototype to do something useful and 4) the person who polished the idea into a useful tool that everybody can and would want to use. Or for lack of better words: brainstorm, prototype, utility, ubiquity. Until an idea or method reaches ubiquity, it's not really considered significant enough to warrant a special name. The have many cases of the history of science of interesting but useless discoveries. Don't believe me? Just peruse the number of articles in the literature with 1 citation or less.
Now, when one person takes an idea from brainstorming all the way to ubiquity, there's no question about who discovered the idea. The problem is when different people partake in the process.
Take brainstorming. The classic example of the brainstorm is the idea of parity violation for the weak interaction, the interaction that was postulated to hold a electron to a positron in order to make a neutron. This was needed to explain the commonplace disintegration of neutrons to protons that is observed in many radioactive materials. The parity violation of the weak interaction was traditionally attributed to the theorists Lee and Yang. However, the story of the discovery of the parity violation of the weak interaction goes that in a particular conference in the 60's, which Lee and Yang attended, there was a lively discussion the nature of the weak interaction. During the first night, Richard Feynman and his room-mate Martin Block continued the discussion when Block blurted out, "maybe parity is not conserved". Feynman pooh-poohed this idea, but suddenly stopped and realized that this could be one of those ideas that seem so stupid it just be right. The next day, Feynman brought this up. Lee and Yang who had been working on the weak interaction, slowly came to the conclusion that there was merit to the idea and after careful study of the literature, realized that no one had actually tested parity violation in the weak force, even though it had been done many times for electro-magnetism and the strong force. So they wrote up a famous analysis of the parity violation, with a proposed experiment. Their friend, Wu, one of a handful of influential female physicists broke off her honeymoon to run the experiment. And thus, the physics community found that one of their fundamental symmetries of nature was violated.
Who then discovered parity violation? Block clearly had the original idea, Feynman conveyed it, and Lee and Yang developed a prototype of the idea. It was then Wu who actually got it working as an experiment. Only after it was experimentally proved, was this hailed as one of the great moments of physics. Block, Feynman, Lee, Yang and Wu all partook in the childbirth of the idea. But due to the stature that Lee and Yang already had in beta-decay studies, their part in the drama propelled them to a Nobel Prize.
A more interesting case is the discovery of the positron. When Paul Adrien Dirac first discovered the relativistic equation of the electron, he realized that it entailed the possibility of a particle just like an electron but with a positive charge. Since no one had observed anything like that before, Dirac conjectured that this was really a shrouded description of a proton, even though a proton was many times heavier than an electron. Indeed the belief in the non-existence of a positron was so strong, Dirac explained the positive particle as a "hole" in an unseen sea of virtual electrons.
Many years later, Carl Anderson was credited with the actual discovery of the positron when he photographed in his bubble chamber the tracks of a particle that had a positive charge but the mass of an electron, as deduced by the curvature of the track in a known magnetic field. However, before Anderson, similar particles had also been observed in cloud chambers that measure tracks from cosmic rays except no one knew exactly what they were. Nevertheless, without Dirac's equation, no-one would have the framework to understand how positrons fit in to the scheme of things. Dirac was allegedly quite upset to find out that an actual positron was discovered because he had hoped his equation also described protons, the other important constituent of a normal atom. This was a case where Dirac had discovered everything about the positron except believing that it exists.
An example close to home is the concept of the funnel in the energy landscape of a protein. The idea of a funnel energy landscape is that there are many conformations of a protein at high energy but at progressively lower energies, there are fewer conformations. Thus an unfolded protein naturally falls into the lowest conformations. The idea of the energy funnel solves the infamous Levinthal paradox that had plagued protein theorists for 2 decades. Although the actual term "funnel" was coined by Peter Wolynes, my former boss, Ken Dill, wrote an earlier paper that demonstrated this very idea using 2 dimensional lattice models but he did not use the term 'funnel' in the paper. History shows that the term 'funnel' stuck. Still, Ken always cites his paper for the definition of 'funnel' whereas Peter cites his paper for the first coinage of the term. Depending on who you to talk, someone different discovered the energy "funnel" concept of protein folding.
The thing is, in research, good ideas are a dime a dozen. I learnt this the hard way. In gradschool and the various postdocs I've had, when I'd have a idea for a new idea and tried to pitch to my boss, more often than not, they'd try to shoot it down. They'd look for flaws or sometimes veto it with their hard-earned intuition. They were pathologically opposed to shiny new ideas. I used to think that it was because they were old fuddy-duddies, grown foggy and conservative by the grinding process of tenure. But I now realize they were resistant for a very good reason. This was because in reality, new ideas are cheap. In the course of supervising generations of students and postdocs, they must have been pitched thousands of seemingly clever ideas that came to naught. It was thus experience that taught them to be skeptical of novel ideas.
What I've found that presenting new ideas to the boss is a multi-stage process. The first step is to propose the idea and watch it get shot down. Then, in my spare time, I'd actually develop a prototype. A prototype is kind of messy and poorly articulated of the original idea. I'd plead for the potential of the idea but chances are the boss would be a little more intrigued with the prototype but overall dismissive. But with a prototype, I could then finally apply it to a real system. I've learnt best to keep my mouth shut until I could bring the boss some actual results applied to a real system. Then we'd talk about it and reach some kind of wall and I'd disappear again. Wash, rinse, recycle.
The tipping point would come when my boss would burst into my office and tell me how he'd figure out something crucial that had been missing in my explanation. Of course, that would be the very thing I'd tried to say at the very beginning, but it would be boorish of me to mention it now. The trouble has always been that communicating a mal-formed idea is not a very effective process. But you can't really clarify an idea without actually building a prototype. What is really happening is that in the to-and-fro between me and my boss, we had developed a mini-language to talk about the original spark of an idea. Only when we had a shared language through building a prototype is the idea actually communicated. Indeed, what had happened here is but a mini recapitulation of the stages of discovery – brainstorm, prototype, application and ubiquity – writ small in the interaction between two people. Application is generating results from which one can think about the idea. Ubiquity is when we both get it.
In the end though, ubiquity is the real test of a scientific discovery. Only discoveries that are useful to a large number of people are significant discoveries. I have no shame in using the word useful in the selling of the science I make. The test of a good article is how many people want to collaborate with you after finding out about it. A little advice that was floated my way from a previous supervisor was that to earn your stripes from postdoc to professor, you've got to find a niche that you, and only you, can do. As a young investigator, it would be suicide to dive straight into an area where you're competing with the big boys, at least at the beginning of your career.
Indeed selling the science well can also make reputations. The physicist Freeman Dyson made his career by carving the rosetta stone between the competing formulations of quantum electro-dynamics of those two giants of postwar physics Richard Feynman, Julian Schwinger and Sin-itiro Tomonaga. These formulations were remarkably different. On the one hand, you have the famously child-like strokes of Feynman diagrams, on the other hand, you have the crushing weight of equations in Schwinger's papers, one of which had the reputation of containing the most number of equations in a Physical Review article for many years. Although Dyson himself admitted that he was not the driving force behind quantum electro-dynamics, he produced a cogent description of electro-dynamics that normal physicists could could use, and his efforts were both appreciated and honored.
Making new discoveries is not simply a matter of serendipidity. Luck falls on the prepared mind. A salty piece of advice comes from the great computer scientist Richard Hamming who noted that the really great scientists were lucky many times over. If you want to be great and receive the blessings of chance when they fall, you have to be ready to receive it. How you ask? Simple, says Hamming, you must always been thinking about the great problems, regardless of whether you can solve them right now or not (Quick: what are the top ten problems in your field?). If you cultivate brilliant collaborators, and learn to listen, then it is inevitable that you will bump into someone who has the idea to crack the insoluble, much as Wu did when she came upon Lee and Yang's paper about the parity violation in the weak interaction. At that moment, you must rush to the quick, drop everything else, and chase that insight to the bitter end. You may even have to cut your honeymoon short.