Veröffentlicht 4. Juli 2013 von Ashutosh Jogalekar

Avram Hershko’s lessons for doing good science

Avram Hershko at Lindau

Avram Hershko – an amiable, mild-mannered Israeli biochemist – shared the 2004 Nobel Prize in Chemistry for his co-discovery of the body’s protein waste disposal system along with Aaron Ciechanover and Irwin Rose. At Lindau Hershko delivered a succinct summary of the discovery of ubiquitin – a protein that essentially tags unwanted and defective proteins and transports them for recycling and destruction to an efficient molecular compactor called the proteasome.

But it was Hershko’s list of lessons for being a good scientist at the end that really caught my attention and that I thought provided a cogent and general offering of advice for young scientists. Here’s his slide:

Hershko’s lessons for doing good science

Valuable lessons, every one of them.

1. Let’s start with the first, the importance of having good mentors: This touches on my thoughts in a previous post on the verbal tradition that has been such an integral part of the training of young scientists for centuries. The responsibility of a mentor goes far beyond simply providing scientific advice and facts. A truly valuable mentor inspires through his passion for science, his uniquely idiosyncratic way of thinking, the informal teaching that goes on outside the lab or classroom, his general interactions with students and colleagues and his guidance for future career directions.

When I was in graduate school I was blessed to have two mentors who were not just world-class scientists but also warm and thoroughly decent human beings. The human lessons I learnt from them – treat everyone from an undergraduate student to a Nobel Laureate with the same degree of respect, make sure that your co-workers and students are acknowledged, give yourself and others the freedom to explore your ideas – perhaps surpass even the very valuable scientific lessons that I imbibed. I continue to be rewarded with outstanding mentors who inspire both scientifically and otherwise, and it is these people who often provide bright spots of light that help me tide over the ups and downs of research which inevitably dot the everyday landscape of science. There is little doubt that a good or bad mentor can make or break your career.

2. Wade through yet uncharted waters that are still shallow enough to navigate: This is another important lesson which echoes through the careers of world-famous scientists. Linus Pauling provides a good example. In the 1920s Pauling travelled to the great centers of physics research in Europe to learn the new revolutionary theory of quantum mechanics. There he met formidable thinkers like Heisenberg, Pauli and Dirac, scientists who were his own age but who had already done Nobel Prize winning work. Pauling was an excellent mathematician, but his skills were surpassed by the mathematical sophistication of the pioneers of quantum mechanics. Pauling wisely realized that while he probably would not be as great a theoretical physicist as Heisenberg or Dirac, he could apply the principles of quantum mechanics to chemistry, a field that was still virgin territory and had few wooers. The rest is history; Pauling provided the first modern theory of chemical bonding and revolutionized chemistry.

But the key lesson to recognize here is the value of applying talents which may not be superlative in one field but which may be unique in another. Pauling’s mathematical sophistication may have been found wanting in theoretical physics, but it was more than adequate to revolutionize chemistry. Pauling’s approach should teach something critical to young students: Identify a field of science where your particular talents have yet to be applied. If you are a mathematician, work in biology and not theoretical physics. If you are a computer scientist, work in neuroscience and not computer science. You are much more likely to make unique contributions to a field where your specific brand of knowledge has still not made a dent.

3. Serendipity: While the value of serendipity in science has almost become a cliche, what is less appreciated is the value of persistence in improving the probability of making a serendipitous observation. When we interviewed 2012 Nobel Laureate Brian Kobilka yesterday, we asked him how he could have possibly hit upon the idea of using antibodies from llamas, of all animals, to stabilize the proteins whose structures got him the prize. Kobilka’s reply was that before he tried llama antibodies, he was already trying out antibodies from virtually every animal, including chickens. Thus, not only was he well-versed with the literature on antibody stabilization of proteins, but he had also made his interest in the technique widely known among friends and colleagues. Thus when he ran into a colleague who was experimenting with llama antibodies at a Gordon Research Conference, his mind was already primed to seize upon the idea. Alexander Fleming’s quip about chance favoring the prepared mind is also a cliche, but it is still exemplified every day by outstanding scientists like Brian Kobilka. Kobilka’s approach also exemplified Pauling’s pithy advice: “To have a good idea, first have a lot of ideas”.

4. Do what is necessary rather than what sounds cool: The value of this lesson in today’s age of technological obsession cannot be overemphasized, and I predict that it will become even more important as we keep on falling in love with the latest technological tools. In his new book, the Russian-born American writer Evgeny Morozov calls this fondness to harness particular technologies mainly because they are available and look attractive as “technological solutionism”. Hershko is in part warning against technological solutionism in the progress of basic science.

A few months ago I wrote about an article by Michael Yaffe of MIT who criticized the use of genetic sequencing tools to address cancer simply because they are increasingly cheap, easily available and fashionable. Hershko’s advice is similar: Don’t use the most state-of-the-art technology to approach a problem simply because it is state-of-the-art. Instead do a careful investigation of available techniques and use that which is most likely to yield results, no matter how primitive or elementary it may seem. The chemist Harry Gray once deflated the results of a sophisticated investigation by simply asking what the color of the resulting compound was, validating the value of that most elementary of all techniques – visual inspection. The 2010 Nobel Prize in physics provides another example of the primacy of primitive techniques; it was awarded to physicists who isolated and studied graphene by using a version of Scotch tape.

Hershko and others’ advice is clear: Don’t be technique-oriented, instead be problem-oriented.

5. Curiosity drives everything: Many Nobel Laureates in this year’s Lindau meeting have driven home the great dividends that curiosity-based research has paid in the annals of scientific discovery. Sadly the current environment of funding in both academia and industry has denigrated curiosity-driven research at the cost of research with immediate practical benefits, unaware or unwilling to acknowledge that the latter critically depends on the former. Fortunately the young minds at Lindau this year have not yet been marred by the mandates of funding overlords, and we can only hope that they will follow their hearts and do what they find exciting rather than what others find practical.

6. Doing is more important than talking and thinking: If we were to rate scientists by the ratio of words said or written to importance of discoveries made, Fred Sanger would undoubtedly be the greatest scientist of all time. The intensely quiet and self-effacing Sanger has been a scientist’s scientist, working obsessively at the bench for three decades and winning two Nobel Prizes for what are undoubtedly two of the most important scientific discoveries of the twentieth century – protein sequencing and DNA sequencing. In the only memoir he ever wrote, a perspective in Annual Reviews of Biochemistry in 1988, Sanger said that “of the three activities of thinking, talking and doing, I am best at the last one”. While working at the bench until the end of one’s career is not a prerequisite for doing great science, many of the best scientists exemplify this tradition. Hershko himself still works at the bench, and so did Max Perutz who was literally working in the lab until the last day of his life. Even if you are not actually working at the bench, it is still wise to stay in touch with the nuts and bolts of science since it is after all these that make the great machine hum. Amazingly, for all his spectacular achievements and absolute dedication to actually doing science, Sanger retired in the 80s and has since spent his days quietly tending his rose garden. For him it was all in a day’s work; loose ends wrapped up, and two Nobel Prizes in the bag.

Ashutosh Jogalekar

Ashutosh Jogalekar is a scientist and science writer based in Boston, USA. He has been blogging at the “Curious Wavefunction” blog for more than ten years, and in this capacity has written for several organizations including Scientific American and the Lindau Nobel Laureate Meetings. His literary interests specifically lie in the history and philosophy of science.