by Luciano Pietronero
Planning scientific discoveries is not like building a railroad. Extreme accuracy in project analysis can sometimes be counterproductive, similar to what happens in Darwinian evolution. The exciting discussion by Doroty Bishop (Nature, 584, 9 (2020)) on how to avoid cognitive biases in scientific and statistical analysis is technically perfect, but still, it can be disorienting if one looks at how significant scientific discoveries are made. I was a young university professor full of enthusiasm and good intentions in the early eighties. I set my optimal rules to referee research projects according to Dorothy’s view. Intellectual honesty, competence, clarity of the objectives and unbiased statistical analysis were the rules which kept me happy for a few years. But after a while, three significant discoveries occurred, all Nobel prizes: The Quantum Hall Effect (QHE) by Von Klitzing, The High Tc Superconductivity by Bednorz and Müller and the Scanning Tunneling Microscope (STM) by Binning and Rohrer. All three were in my field of expertise, and I even knew most of the protagonists.
Well, to my great disconcert, I realized that, as a potential referee of these projects, my “perfect” system of analysis would have led to the rejection of all of them, and with perfectly good reasons. The original project of von Klitzing had little to do with the magic topological properties of the QHE; Alex Muller’s idea of reaching high Tc SC was based on the softening of phonons near a structural instability, but this is not the mechanism. Even the STM was supposed to be a metallurgical tool to explore the surface of metal with a resolution of 500 atoms. Nobody could have predicted that the tip would rearrange to give information at the level of individual atoms.
So I realized my perfect system – honest, unbiased and competent – would have killed all these three discoveries. The lesson I learned was that a too meticulous analysis based on what you know can be problematic to explore what you don’t know. But in terms of positive hints on improving my analysis, there was little to learn. After a few years, an exciting discussion with Stuart Kauffman on how birds can fly gave me some intellectual relief. The Darwinian development of wings was certainly not motivated by the hope to fly because, below a specific size, you certainly don’t fly. The evolutionary line for wings was something else (it seems to balance the running or cooling blood), and only when they reached a specific size did this evolutionary line meet the (unplanned) evolutionary line of flying. Similarly, there was a particular line of research in the three discoveries above, and then, unexpectedly, something else appeared. Müller was looking for High Tc SC but along a line which was somewhat different from the actual one. The merit of these scientists was to go along some lines consistently and professionally but also to realize the new discoveries that suddenly appeared.
Note that something similar happened to Columbus travelling to America (he miscalculated the earth’s radius) and in the properties of the radio by Marconi (he thought radio waves could follow the earth’s curvature). Maybe, after all, this is called serendipity and is a natural characteristic of experimental science.
But also, in theory, a sort of educated bias or intuition seems to play a significant role. Some time ago, I realized that the statistical methods used by cosmologists in analyzing the distribution of visible matter assumed a priori that this must be homogeneous at some scale, so they considered only the question of “when” it becomes homogeneous, but not “if” it becomes homogeneous. Technically, this implied turning the amplitude of a power law correlation into a correlation length, which is a capital sin for those familiar with complex and fractal structures. It was a clear bias which was motivated by different observations. So, we repeated these analyses and found that in all the available samples, the distribution of galaxies did not show any homogeneity. In 1996, at a conference in Princeton, I had a public debate with Jim Peebles (Nobel 2019) and his group. The hall was so crowded that Phil Anderson was not allowed to enter by the security, and I spoke to him only afterwards. He asked me for Peebles’ comments on my arguments. I replied that Peebles argued that I only showed the data in my favour. I wanted to add that instead, I showed all the available data, but Phil suddenly interrupted me by saying: “Of course, what else should one do?”.
A few years later, around 2000, I had another interesting discussion with Phil on the much-debated subject of High Tc SC in Trieste. Phil had argued for several years that the problem was solved by the properties of strongly correlated electrons beyond the Fermi Liquid theory. When I asked him what was, in his view, the active principle for increasing Tc from solid correlation, he answered: “Well, I wish I knew that!”. So, his position was more a prophetic wish than a scientific proposition. Was this good or bad for science? Who knows. The fact is that today, it is still not clear how strong a correlation may increase Tc. Finally, the toast proposed by Phil at the end of each dinner was always: “Against common wisdom!”. And it was not exactly an unbiased point of view.
In summary, scientific discoveries resemble Darwinian evolution, in which one looks for new things in a new space. A strategy too strictly based on what is known may lead to good incremental progress but hardly to a real breakthrough. Elements like an educated bias, interpreted as intuition or creativity, can give an artistic touch and sometimes lead to meaningful results. The evaluation of these elements is intrinsically tricky but for sure, they make the scientific game more fun.