Monday, February 25, 2019

Management lessons not learned from the discovery of graphene

Don't follow the pack!

I just read the Random Walk to Graphene, by Andre Geim. It is the lecture he gave when receiving the 2010 Nobel Prize in Physics. I should have read it long ago but was motivated to read it now because the following sentence features in Joseph Martin's "purloined letter'' argument about why condensed matter physics lacks status.
Graphene has literally been before our eyes and under our noses for many centuries but was never recognized for what it really is.
I learned some nice science from the lecture. Foremost, it is a great story of scientific creativity, perseverance, and serendipity. However, I want to mention a few things that highlight how the story strongly conflicts with most views about how science is currently "managed" and people operate.

Geim starts by recounting his Ph.D. and early postdoc years. His Ph.D papers were cited twice, by co-authors.
The subject was dead a decade before I even started my Ph.D. However, every cloud has its silver lining and what I uniquely learned from that experience was that I should never torture research students by offering them “zombie” projects.
Several years later he worked on a new topic as a staff scientist in Russia.
This experience taught me an important lesson that introducing a new experimental system is generally more rewarding than trying to find new phenomena within crowded areas.
He notes that when after a six-month visiting postdoc in Nottingham he entered the Western postdoc market with an h-index of 1!

When he was in the Netherlands as a young faculty member in a high magnetic field lab he began to experiment in creative directions leading to investigations of "magnetic water" and the iconic experiment of the levitating frog for which he received an Ig Nobel Prize.
we saw balls of levitating water (Fig. 1). This was awesome. It took little time to realize that the physics behind this phenomenon was good old diamagnetism. It took much longer to adjust my intuition to the fact that the feeble magnetic response of water (105), that is billions of times weaker than that of iron, was sufficient to compensate the Earth’s gravity. Many colleagues, including those who worked with high magnetic fields all their lives, were flabbergasted, and some of them even argued that this was a hoax.... 

The levitation experience was both interesting and addictive. It taught me the important lesson that poking in directions far away from my immediate area of expertise could lead to interesting results, even if the initial ideas were extremely basic. This in turn influenced my research style, as I started making similar exploratory detours that somehow acquired the name “Friday night experiments.” The term is of course inaccurate. No serious work can be accomplished in just one night. It usually requires many months of lateral thinking and digging through irrelevant literature without any clear idea in sight. 
The story of the discovery of graphene using cellotape [Scotch tape, sticky tape] was more complicated, circuitous, and involved a lot more hard work than I realised.
There were two dozen or so [friday night] experiments over a period of approximately 15 years and, as expected, most of them failed miserably. But there were three hits, the levitation, gecko tape, and graphene. 
The story of the first publication is interesting. It took nine months to get the paper into Science.
First, we submitted the manuscript to Nature. It was rejected and, when further information requested by referees was added, rejected again. According to one referee, our report did “not constitute a sufficient scientific advance.” Science referees were more generous (or more knowledgeable?), and the presentation was better polished by that time. In hindsight, I should have saved the time and nerves by submitting to a second-tier journal, even though we all felt that the results were groundbreaking.
This is consistent with my belief that there is not a lot of correlation between great discoveries and publication in luxury journals.

So what should we learn from this story?
First, we should all be a little more adventurous and take some risks and explore new areas. Previously, I have argued successful researchers should move onto new hard problems. 
A lot of this relates to diminishing returns and opportunity costs.
Yet, unfortunately, there are now significant institutional and cultural pressures against this. However, I think senior faculty have a responsibility to buck these trends.

Second, funding agencies and university management really need to learn from this story of graphene. It really goes against metrics, KPIs, short term goals, making people "accountable" for extremely well-defined timetables and research outcomes, and forcing/hiring people to work on the latest hot topic.

Graphene is cool! And I am sure that there is a lot that remains to be discovered about graphene. However, I find it disturbing that so many people have flocked to the field. A few years ago I met a faculty member from Manchester and they said they were on the out because they were not working on graphene and there was a lot of pressure for people to be working on it.

There is another side to the story that I am not sure what to make of which has an Australian connection. When Alan Gilbert was vice-chancellor at the University of Melbourne he tried to build a parallel private for-profit institution, Melbourne University Private. This turned out to be a massive failure, wasting hundreds of millions of dollars. In 2004 Gilbert moved to Manchester as Vice Chancellor. Of course, his main goal was to lift Manchester in the global rankings.
The Wikipedia page about Gilbert states,
According to the university's strategic plan[8] (largely a copy of his [Gilbert's] earlier and now abandoned Melbourne Agenda (2002)[9]) the university aims to have five Nobel Laureates on its staff by 2015, at least two of whom will have full-time appointments, and three of which it is intended to secure by 2007. During Gilbert's tenure as vice chancellor, a Nobel Prize winner in economics, Joseph Stiglitz, was appointed the head of the Brooks World Poverty Institute at Manchester, and Sir John Sulston was appointed to a chair in the Faculty of Life Sciences. After Gilbert's death Andre Geimand Konstantin Novoselov, both of whom were appointed before Gilbert moved to Manchester, were awarded the Nobel Prize for Physics in 2010.
From the little I know about Gilbert it is very hard for me to see how he would have supported Geim's approach to doing science, particularly given that there were not well-defined immediate benefits to the corporate sector.


  1. In full agreement with your suggestion that established faculty should take risks and venture into new areas. The problem is when one is in the career advancing mode based on metrics, funding etc, the time for observant research with intuition like the the one you have mentioned for graphene is overlooked as there is a great rush to publish. There should be a separate window of funding for high risk research for established faculty.


    The last lines relevant to "Don't join the pack"

    I shall be telling this with a sigh
    Somewhere ages and ages hence:

    Two roads diverged in a wood, and I—
    I took the one less traveled by,
    And that has made all the difference.

    Poem attributed to Robert Frost.

  3. Group think of Sabine Hossenfelder is very much operative in universities , research institutes world wide. It is very difficult to survive in academia and research without being in the pack (group). Being a lone genius in modern academia and research is difficult.

    Here is the Group think video by SH

  4. Thanks for sharing the video. 2 minutes worth watching. It is very relevant.