Learning from anomalies and discontinuities.

Many of our scientists and engineers are generally comfortable in status quo. Most of us are happy with organized research. A problem is posed and a solution is found. We use all the known tools of science, theoretical and experimental, be they instrumental, which span an amazing range of length and time scales or computational, whose power and reach are becoming mind-boggling. Invariably, we develop models and theories and try to fit the experimental data or we do vice versa.

When the models fit the experiments, we are all happy. The student is happy, since he can finish his PhD thesis in time and, perhaps seek his postdoctoral in that land of opportunity, namely USA. The guide is happy, since he feels here is one more of his contribution to the pool of scientific knowledge, and also because one more research publication is under his belt. The referee of the paper is happy, since the theory or model fits the experiment; surely if there is a fit, both the theory and the experiment must be right! He does not have to stretch himself. The editor is happy too, since he is not publishing a paper, which is likely to raise controversies. So this is the happy zone, a comfort zone!

But what about those problems, which are not in the comfort zone? Those unresolved problems, which have been crying for answers for years, but are too risky to try. What about those observations, which look anomalous, since they go beyond what would be expected by common sense? What about those sudden discontinuities which appear on the horizon? When a theory or a model is developed, most points fit the line of prediction, but some data falls outside. Are these just experimental aberrations, or is there a deep message in them, which can open up a new frontier? It is my feeling that many of us leave such things alone, like a fast rising ball outside the off stump. We do know that trying to hit it can bring rich rewards but there is a danger of getting caught behind too! I am going to persuade you to believe that there are a lot of rewards in taking those risks and moving out of our comfort zones to solve problems that are challenging and risky at once.

Sometimes serendipity knocks on your door

Let me now come to the issue of serendipity or lucky accidents and Indian science. As we know, sometimes we reach unknown destinations accidentally. This has happened for centuries. In 1786, Luigi Galvani noticed the accidental twitching of a frog’s leg and discovered the principle of electric battery. In 1858, William Henry Perkins was trying to synthesize Synthetic quinine from coal tar and he came across a colored liquid, a synthetic dye. This was the beginning of the modern chemical industry. Leo Bakeland was looking for synthetic shellac and he accidentally found Bakelite. That was the beginning of the modern plastics industry. In 1929, a gust of wind blowing over Alexander Fleming’s moulds, as we know, created the new antibiotic age. As a proud Indian, it worries me as to why such a wind did not blow over the laboratories of Indian innovators! Why did we not get one breakthrough, which had the potential to lead India to such a new industry or even an entirely new product through such accidents? Does this mean that those lucky accidents did not at all take place in India? Or if they did take place, were we equipped enough to spot them? What should not be forgotten is that a trained mind is required to spot these accidents. Eyes do not see what the mind does not know. Perhaps there are other reasons. Let me explain this through our own experience.

In mid-Eighties, I was in Delhi, when I saw the front cover of an issue of Nature carrying this beautiful photograph of spatio-temporal patterns on gels, which were discovered by Tanaka from MIT. I was fascinated, since we had never noticed these patterns. I took a xerox of this cover page, brought it to Pune, and showed it to my PhD student. I told him, "look at what Tanaka has discovered for the first time and he has made it to the cover page of Nature. I wish we had discovered these strange patterns, we would have also made it to Nature". He looked at me and said, "but sir, I had observed these two years ago". I was shocked. I said, "why did you not tell me about them"? He said, "sir, I thought it was not something normal. So I did not tell you". I trust in his answer lies the malady of Indian science. We are so much in search of the "normal" that the abnormal frightens us. The lucky accident did happen in an Indian laboratory, but the one who saw it was too scared to see the significance of it. Anyway, we got all our students together and told them the importance of such observations. We told them how major breakthroughs have taken place because of people looking for and sometimes when they get lucky, actually noticing such accidents. Here was a cultural shift and it did pay a rich dividend, but almost 10 years later.

Sometimes serendipity knocks on your door, but you do not hear it. The discovery of cynoacrylate adhesives, popularly known as Superglue, is a classical case. Harry Coover of Eastman Chemical Company was assigned the problem of finding an optically clear plastic from which precision gunsights could be cast. He was working with some cyanoacrylate monomers, which showed promise, but he was plagued by a recurring problem: everything these monomers touched stuck to everything else, which he recorded. However, he didn’t see this as serendipity, just as a severe pain! He was thinking about gunsights, and nothing but gunsights. The adhesive qualities of these monomers were a serious obstacle in his path. The research was successful, but the end of the War brought this project to an end. He forgot the stubbornly-sticking cyanoacrylates. Serendipity had knocked, but he did not hear it.

Moving ahead a few years to 1951, there was a need to discover stronger, tougher and more hear-resistant acrylate polymers for jet plans canopies. Coover was now supervising a new crop of eager young chemists who were investigating the properties of the same cyanoacrylate polymers that he had been working with earlier. The monomers were difficult to make, even more difficult to purify and still more difficult to analyze for purity. Someone in the group prepared what he thought was a pure sample of ethyl cyanoacrylate and decided to measure its refractive index in order to characterize its purity. The measurement was made and recorded. When the scientists attempted to separate the prisms, they could not! They were worried that the refractometer was ruined. Coover, however, suddenly realized that what they had was not a useless instrument, but a unique adhesive. Serendipity had given him a second chance, but this time his alert mental process led to inspiration. Immediately, Coover asked the scientists for a sample of his monomer and began gluing everything he could lay his hands on—glass plates, rubber stoppers, metal spatulas, wood, paper, plastic—in all combinations. Everything stuck to everything, almost instantly, and with bonds that could not break apart. In that one afternoon, cyanoacrylate adhesives were conceived, purely as the result of serendipity. These adhesives not only had a significant impact on consumer and industrial applications, but also became a promising answer to a surgeon’s dream of a tissue adhesive.

Choose interesting problems

If you analyze the winners in science, very often, you find that they are ones, who chose interesting problems. A key is in the ability to pose, rather than merely solve, high-level problems. Solving an easy problem has a low payoff, because it was well within reach and does not represent a real advance. Solving a very difficult problem has a high payoff, but frequently it may not pay at all. Many problems are difficult because the associated tools and technology are not advanced enough. For example, one may do a brilliant experiment but current theory may not be able to explain it. Or, conversely, a theory may remain untestable for many years. Thus, the region of optimal benefit lies at an intermediate level of complexity. These intermediate problems have the highest benefit per unit of effort because they are neither too simple to be useful nor too difficult to be solvable. Today’s competitive science is based on this domain. But there is no substitute to focusing energy on these difficult problems, which have a handsome pay off in the long run.

(To be continued in the next issue)

RA Mashelkar