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DBL%20Hendrix%20small.png College chemistry, 1983

Derek Lowe The 2002 Model

Dbl%20new%20portrait%20B%26W.png After 10 years of blogging. . .

Derek Lowe, an Arkansan by birth, got his BA from Hendrix College and his PhD in organic chemistry from Duke before spending time in Germany on a Humboldt Fellowship on his post-doc. He's worked for several major pharmaceutical companies since 1989 on drug discovery projects against schizophrenia, Alzheimer's, diabetes, osteoporosis and other diseases. To contact Derek email him directly: Twitter: Dereklowe

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« Not in My European Back Yard | Main | From Each According To Their Creativity, To Each According To Their Difficulty? »

January 28, 2004

The Best Bad News He Ever Had

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Posted by Derek

The January 22 issue of Nature has a fine essay by Freeman Dyson (a hero of mine, I should add) about a fateful meeting he had with Enrico Fermi back in 1953. This was back when Dyson was a professor at Cornell, studying both the weak and strong nuclear forces.

There was a fine theoretical framework for the weak force (quantum electrodynamics, and a fine one it remains to this day.) But the strong force was giving people fits. Fermi was leading a team that did the first accurate measurements of the scattering of mesons by protons, the best data available on what the strong force was like. And after showing that QED did an excellent job on the weak force, Dyson had put his theoretical group to work in this trickier area.

After what he describes as "heroic efforts" (recall that these were the days long before any meaningful computing capacity), Dyson's team had a set of graphs of what the meson-proton interactions should look like, and they weren't too far off of Fermi's experimental data. So Dyson excitedly set up a meeting with Fermi in Chicago, showed him the graphs, and I'll let him take the story from there:

. . .he delivered his verdict in a quiet, even voice: "There are two ways of doing calculations in theoretical physics", he said. "One way, and this is the way I prefer, is to have a clear physical picture of the process that you are calculating. The other way is to have a precise and self-consistent mathematical formalism. You have neither."

. . ."To reach your calculated results, you had to introduce arbitrary cut-off procedures that are not based either on solid physics or on solid mathematics." In desperation, I asked Fermi whether he was not impressed by the agreement between our calculated numbers and his measured numbers. "How many arbitrary parameters did you use for your calculations?" I thought for a moment about our cut-off procedures and said "Four." He said "I remember my friend Johnny von Neumann used to say, with four parameters I can fit an elephant, and with five I can make him wiggle his trunk." With that, the conversation was over.

Dyson points out that, in hindsight, Fermi was absolutely correct. The theory they were trying to use could not possibly have done the job, not least because no one had a good idea of what protons were like (Gell-Mann hadn't come up with the concept of quarks.) Fermi, of course, was dead before quarks had ever been postulated, but he could tell that the existing framework was inadequate. And he saved Dyson years of what would have almost certainly been wasted time.

This is a perfect example of one of Weinberg's "Golden Lessons" that I spoke about on January 20th (below.) If you're working on a problem that no one (yet) has the power to solve, you can spend all your creativity in vain. Think of what would have happened if, say, Isaac Newton had stumbled across radioactivity. What could he have made of it? What are the odds that he would have been even close to correct? (And keep in mind, I'm saying these things about one of the greatest natural talents that science has ever known - Newton was downright terrifying.) A mark of a really great scientist, which Fermi certainly was, is to have a better eye for what problems are both significant and soluble. That's a small territory to work in sometimes.

In drug research, we work against a backdrop of doubts like this. Extraordinary new things are learned about living systems every year, and every time I find myself pitying all the people who were working on the same problem years ago. They may have suspected, but couldn't have know, what was really happening. Years from now, other scientists will pity us in turn. All the more reason to celebrate, when we actually get something to work!

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