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Apprentice to Genius: The Making of a Scientific Dynasty by Robert Kanigel

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Key Takeaways

  1. Johns Hopkins has adopted this mentor / mentee relationship. Student --> apprentice --> protege --> mentor
    1. Any scientist of any age who wants to make important discoveries must study important problems. But what makes a problem important? And how do you know it when you see it? The answers don't come from reading them in a book, nor even by explicitly being taught them. More often, they're conveyed by example, through the slow accretion of mumbled asides and grumbled curses, by smiles, frowns, and exclamations over years of a close working relationship between an established scientists and his or her protege
    2. One crucial task of early adulthood is finding a mentor. A major satisfaction during midlife is being one. The mentor functions as a mixture of parent and peer. Typically older than his protege by about half a generation. Most of all, the mentor fosters the young adult's development by believing in him, sharing the youthful Dream, and giving it his blessing
    3. But what, precisely, gets passed on? Certainly not just specific knowledge and technique; indeed, these may be the least of it. It isn't knowledge or skills that apprentices acquired from their masters so much as a "style of thinking", as one laureate in chemistry told her. It was problem-finding as much as problem-solving. Those future Nobel laureates were being socialized, to use sociology's vocabulary, into a sense of the significant, or important, or right problem. Don't bother with the routine specific problems. Leave them to others. Don't bother, either, with big, fundamental problems that are simply not approachable with available techniques and knowledge; why beat your head against the wall? Half the battle is asking the right question at the right time - when it's neither premature to tackle it, nor invites too obvious an answer, when the right methodology is at hand, when enthusiasm is at its peak. And then, just do it! Don't spend all year in the library getting ready to do it. Don't wait until you've gotten all the boring little preparatory experiments out of the way. Don't worry about scientific controls, except the most rudimentary. Just go with your hunch, your scientific intuition, and isolate that simple, elegant, pointed experiment that will tell you in a flash whether you're on the right track
    4. It takes about the same amount of effort to work on an important problem as a trivial and pedestrian one
  2. Brodie
    1. "Pull a Brodie" - take a risk of a long shot, to go for it
    2. Brodie was the godfather of drug metabolism
    3. Brodie had a monstrous work ethic, skipping sleep for nights on end when he felt close to a discovery. There was no separation between work and play, the lab and home; time did not break neatly into days and hours
    4. Axelrod and Brodie were responsible for discovering Tylenol - That was the beginning. Not it was real science, no more mindless measurement. This was research - probing the unknown, making discoveries. Here, hunches counted. There was no book in which to loop up the answers because you were writing the book, you were finding the answers. You had to be at home with ambiguity and uncertainty
  3. Shannon
    1. James Shannon started NIH, the most accomplished and prestigious government department - the best boss anyone ever had, a diamond clear intellect, cool, developed a sense of urgency, competitive yet collaborative, the best people, personal excellence in everything he did, no mediocrity, amazing leader (the Kind of man accustomed to working with and through others to achieve his ends), you could feel his presence and he had a way of getting the most out of people
    2. He had absolute confidence I could do anything, Brodie remembers fondly, and that made me do it. It was great psychology
    3. Shannon was a man whose ego was satisfied if the people he picked did well. He got the credit eventually, of course, but he got it by giving.
    4. Many people said they had never worked at a place where the concentration of talent was so high.
    5. Didn't look for credentials, but ability to spark excitement in others
  4. Axelrod
    1. Julius Axelrod was a noble prize winner. Most tend to lock themselves away after something prestigious like this, but Julius didn't. He didn't even have an office. He wasn't professor Axelrod, he was Julie. Not only could I see him, I ate lunch with him nearly every day and I could ask him any question I wanted, even stupid ones
    2. Axelrod gave new colleagues a problem at which they were apt to do well, yet not so apparent as to be trivial - small wins are insanely important. The strategy worked
    3. You've got to ask it before it becomes obvious
    4. All you needed were good ideas and the willingness to try them. What you didn't need and didn't want was too exhaustive a knowledge of the existing literature - because, as one former student puts it, "all it can do is tell you what you can't do." As in so many areas of his scientific style, it was as if Steve Brodie were speaking across the generations, or at least down from the 7th floor of Building 10. You don't learn anything by thinking about what to do, just by going into the lab and doing them. You have to be ready to drop a cherished theory, no matter how long you've worked at it. You can't get too emotionally involved. You have to give up in the face of facts. He was infinitely adaptable, at home with ambiguity, willing to go wherever the wind took him
    5. Julie plays with ideas like kids play with toys
    6. By every account, he was a master at reducing complex questions to simple experiments with clear answers
    7. "I wasn't a hard worker. I'd leave most afternoons around 4 or 5 (on Friday's even earlier) and at home I'd read newspapers, books, magazines, but I'd often be thinking about my problems. Essential to research success is not outstanding scholarship, nor exceptional intelligence, but rather motivation and commitment. This doesn't necessitate being in the lab day and night, but you think about the problems you are currently working with all the time, no matter what other activity you are engaged in.
  5. Snyder
    1. When building up my lab, I took the approach of my mentor, Axelrod: Don't get hardening of the scientific arteries by filling permanent staff positions. Rather, take on young PhD students and postdocs, keep them a few years, and periodically rejuvenate with a new crop
    2. Sol's approach is never to establish an end point ahead of time. He goes where things take him. He'll revise plans, make a lot of whatever's there. He'll take a flier

What I got out of it

  1. One of the best "coaching" books I've read. The passing down of not only problem-solving, but problem-finding is so key. Working on important problems, building a high-functioning team, being open and comfortable with ambiguity. This is an amazing startup and leadership book that happens to focus on scientific discovery