Lessons from the discovery of liquid crystals

I recently learned a little about the history of the discovery of liquid crystals, stimulated by Soft Matter: A Very Short Introduction by Tom McLeish. Besides being a fascinating story there are lessons about the importance of curiosity-driven research, interdisciplinarity, serendipity, and the long road to technology.

Friedrich Reinitzer (1857 - 1927) was a botanist and chemist who worked at the Institute of Plant Physiology in Prague. He was studying cholesterol with the aim of determining its molecular weight. He produced crystals of cholesteryl benzoate and measured their heat capacity as a function of temperature. Aside: For chemists today this measurement is known as differential scanning calorimetry (a constant source of heat is added and the temperature measured as a function of time). 

In 1888, Reinitzer observed that the crystal melted at 145.5 degrees Celsius (signified by absorption of heat), forming a milky liquid. However, at 178.5 degrees Celsius, there was a second absorption of heat, and the liquid became transparent. This suggested that there were two melting transitions. Puzzled by this Reinitzer consulted the physicist and crystallographer, Otto Lehmann, who promoted the idea that this was a new state of matter, which he dubbed a "liquid crystal" (or flowing crystal).

Today, cholesteryl benzoate is classified as a chiral nematic liquid crystal, which is also sometimes known as a cholesteric liquid crystal, in honour of the first one. A schematic of the ordering is shown below.

The milkiness was not explained until the 1960s by Pierre-Gilles de Gennes, who exploited an analogue with a superconductor in a magnetic field.

More detail is in the paper

Liquid‐Crystal Science from 1888 to 1922: Building a Revolution 

Michel Mitov 

This discovery of liquid crystals was the first of many cases where a new state of matter was discovered by a thermodynamic measurement. Others include superfluid 4He (the lambda transition) and superfluid 3He, as I have recently highlighted.

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 ($\sim$${10}^{}$${}^{}$${}^{}$), 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.

In praise of modest goals

Maybe it is just my personality but I increasingly find that in science and life I am out of step with the surrounding culture. I just have modest goals.  I just want to understand a few things and make some sort of reliable contribution. This means publishing in PRB, J. Chem. Phys., and occasionally in PRL. I don't aspire to publish in luxury journals, double my funding, to see my university the most highly "ranked" in Australia, or claim that my research will revolutionise materials science and molecular biology, ...
This is why I increasingly find it hard and tedious to write grant applications.
I will also be happy if Liverpool just finish in the top 4 of the Premier League....

I think good science is really hard and most advances come from long term projects with painstaking hard work and from the occasional serendipity.

Yet it seems society is sold on hype, the winner takes all mentality, and everyone should aspire to be a winner...

I am certainly interested in big questions and grand challenges. But I feel I am realistic about what contributions I and others (even the extremely gifted and well funded) can make. It is generally the long slow road. Earlier I posted about how I am skeptical and left cold by "big hairy audacious goals".

Here are a few of my inter-related problems with many of the goals and ambitions I encounter.

1. Many I find simply unrealistic, either scientifically, politically, or economically.
Furthermore, when I look at the ambitious goals that were hyped 5, 10, 20, and 30 years ago I see they have failed.

2. Many, particularly young, people are left feeling like "failures" because they did not "succeed" by becoming the "best", e.g. by publishing in a luxury journal.

3. They divert resources (time, energy, money, and talent) away from modest goals that may produce more actual fruit in the long term.
I think MOOC's, topological insulators, string theory, AdS-CFT, topological quantum computing, iron-based superconductors .... are all interesting and worth a few select groups playing around with. But I fail to see the justification for hordes of people working on them.

4. They can easily degenerate into fantasy and hype.

5. Some of these ambitious enterprises become institutionalised to the point that defending the "vision" leads to propaganda and an unwillingness to listen to criticism and change course. Peter Woit's blog does a nice job of showing how this is the case for string theory. Here are two other examples, from social activism.
Teach for America has the laudable goal of attracting gifted and privileged graduates to teach in poorly resourced schools. However, an article documents the incredible lengths they go to in order to mute negative publicity.
Microfinance is a great initiative that helps alleviate poverty in the Majority world. However, when two MIT economists, the authors of Poor Economics, did a systematic study of its effects, they found that it produced modest but tangible benefits. Unfortunately, they were roundly attacked by some not-for-profits because the study contradicted their grand claims that microfinance was completely transforming the lives of recipients.

But, maybe it is just my personality ...

Addendum: Reflecting on this more and starting teaching last week I realised that having modest goals for teaching and for seminars is also relevant. As one gets more experienced one realises just how little students (and seminar audiences) actually learn and understand. Hence, although I teach at a "high level" I try to make sure really basic points and skills are hammered home. Similarly, David Mermin's goal for a colloquium is modest.

Serendipity remains the best quantum materials discovery method

Materials by design has long been a holy grail of computational materials design. The idea is that one could predict both the chemical composition, structure, and desired functional physical properties of materials based on "ab initio" electronic structure calculations.

There is a nice Physics Viewpoint, "Materials prediction scores a hit", by Filip Ronning and John Sarrao. The two pages are worth reading and digesting. The authors puts in context the recent successful prediction of superconductivity in a high pressure phase of iron tetraboride.

Why is predicting superconductors so hard? Particularly, in strongly correlated electron materials? It is a problem with multiple energy scales. Basically, superconductivity is an emergent low-energy phenomena that is an instability in a metallic state, that itself involves emergent low-energy scales.

Given the above one can debate the merits of the White House Materials Genome Initiative, but be excited about the recently announced $90 million dollar initiative "Emergent Phenomena in Quantum Systems" of the Gordon and Betty Moore foundation. The focus is on Quantum materials with a significant emphasis on solid state synthesis.

A circumstantial discovery

At the conference in Bangalore last week, Jeremy Levy (U. Pittsburgh) gave a fascinating talk about a significant new discovery that allows one to fabricate nanoscale electronic circuits at the interface between two transition metal oxide materials. (as described in this Science paper)

There were several things that were circumstantial about this discovery.

* Jeremy had tickets to the 2006 World Cup Final in Germany. This led to a visit to Augsburg that stimulated the original ideas.

* As a kid, Jeremy had played with

Etch A Sketch and understanding how it works inspired the basic idea on how to "write" the circuit onto the interface.

* The original fabrication was not done under vacuum but in air. It turned out that the water vapour present was essential to inducing charge carriers into the interface.

When I started writing this post I thought the discovery involved serendipity, but that involves more when one is looking for something different.

Quantum tunneling of protons in small molecules

A really nice article, Houdini molecule escapes energy trap, in Chemistry World last year sat in my "enzyme paper" folder. I just read it today. It is a fascinating story of beautiful science including serendipity, and a healthy interaction of theory and experiment. The News and Views piece and the Nature paper are also worth a read.