主题：【文摘】A Strategy for a Successful Scientific Career -- 不爱吱声

I had used a different strategy. My approach had been that of predicting how a particular biological process might work and then taking years to test whether my guess might be right. This was enormously risky. The good news was that I was carrying out experiments that were different from those being done by everyone else. The problem was that these tests could produce only a \\\\\\\\\\\\\\\'yes\\\\\\\\\\\\\\\' or \\\\\\\\\\\\\\\'no\\\\\\\\\\\\\\\' answer. If \\\\\\\\\\\\\\\'yes\\\\\\\\\\\\\\\', I might be able to add something unique to the world\\\\\\\\\\\\\\\'s store of scientific knowledge. But if \\\\\\\\\\\\\\\'no\\\\\\\\\\\\\\\', I would learn nothing of real value — in this case, I could eliminate just one of the many possible ways in which DNA replication might begin.

I wanted to continue to focus on how DNA is replicated for my postdoctoral work in Geneva. But what strategy should I choose? The months of analysis triggered by the wake-up call of my PhD failure finally produced an answer. I would look for a unique experimental approach, but one that would have a high probability of increasing our knowledge of the natural world, regardless of the experimental results obtained.

After a great deal of soul-searching, I decided that I would begin by developing a new method — one that would allow me to isolate proteins required for DNA replication that had thus far escaped detection. I knew that the enzyme RNA polymerase, which reads out the genetic information in DNA, binds weakly to any DNA sequence — even though this protein\\\\\\\\\\\\\\\'s biologically relevant binding sites are specific DNA sequences. If the proteins that cause DNA to replicate have a similar weak affinity for any DNA molecule, I would be able to isolate them by passing crude cell extracts through a column matrix containing immobilized DNA molecules.

Arriving in Geneva in late 1965 with my PhD degree finally in hand, I found that by drying an aqueous solution of DNA onto plain cellulose powder, I could construct a durable and effective \\\\\\\\\\\\\\\'DNA cellulose\\\\\\\\\\\\\\\' matrix. A large number of different proteins in a crude, DNA-depleted extract of the bacterium Escherichia coli bound to a column containing this matrix. Moreover, these DNA-binding proteins could be readily purified by elution with an aqueous salt solution. Using this new biochemical tool and a large library of mutant T4 bacteriophages obtained from Dick Epstein in Geneva, I discovered the T4 gene 32 protein after moving to Princeton a year later as an assistant professor. This proved to be the first example of a single-strand DNA-binding (SSB) protein, a structural protein that plays an important role in DNA processes in all organisms (see Nature 227, 1313−1318; 1970).

The strategy of investing in method development and then using this new method for a major series of experiments would be employed over and over again during the next 25 years of my career as a research scientist. As a result, my laboratory almost never felt that it was in a race with other laboratories, and our successes were sufficient to satisfy both me and many of the graduate students and postdoctoral fellows who would join my laboratory. It seems strange to recall that we may owe all it all to one very unhappy PhD thesis committee at Harvard, nearly 40 years ago.