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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: derekb.lowe@gmail.com Twitter: Dereklowe

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In the Pipeline: Don't miss Derek Lowe's excellent commentary on drug discovery and the pharma industry in general at In the Pipeline

In the Pipeline

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May 6, 2002

So What's A Worthwhile Problem, Anyway?

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Posted by Derek

My last post naturally leads to that question. I can only speak for my own specialties, organic and medicinal chemistry. An example of really worthwhile problems in the former would be (to pick a few at random): how to form quaternary carbon chiral centers, how to get metal-catalyzed couplings to work more generally and reproducibly, a new inexpensive method to make unnatural amino acids, or a way to turn the nitroaldol reaction into something generally useful.

Examples of worthwhile problems in the latter field would be: how to make good phosphatase inhibitors, how to predict better what sorts of compounds will be absorbed out of the gut into the bloodstream, how to make new things that can substitute for a peptide bond, or how to approach compounds that interfere with protein-DNA interactions.

It's not like no one's worked on these; there are ideas and partial solutions to most of them. But a real advance in any of these areas would be welcomed by plenty of people, and recognized as a significant achievement.

Making lists like that is easy. What about things that have no obvious use? I'm still in favor of those, because the history of science has shown over and over that you can never tell what oddities may turn out to be useful. There's a lot of curiosity-driven research that gets done on projects like these.

So what isn't worth doing? Doing something that's already been done, because everyone's doing it or because you can't think of anything else for one. Doing things that (even if they worked) have already been superseded by techniques available when you started.

And examples of those? Here's where I bring in the fan mail! Things in organic synthetic chemistry that I wouldn't consider worth the effort might include: total syntheses of large natural products that add no new methods to the literature, adding yet another Lewis acid to the long list of the Lewis acids that can be used to, say, form acetals from aldehydes, or similarly coming up with yet another way to dehydrate an aldoxime to a nitrile. But you can pick up chemical journals from the last year and find all these things, and likely worse.

I'll forebear, for now, listing things that I don't think are worth doing in medicinal chemistry, for fear that I'll go to work tomorrow and find that someone wants to do one of them. My point is that many of these dud problems could nonetheless occupy your time, have their high and low points, their challenges and solutions, just like a real research project. If you didn't know better, you'd think you were doing something useful. You could spend nights and weekends on some of these things, and to the untrained eye you'd be getting an awful lot of work done. But to no point.

Of course, one reason I can have this attitude is that I've spent time on such things myself. It's only with time that I've come to see that science is so intrinsically tricky and interesting that almost anything can fill your hours and engage your mind. But isn't it better to find yourself getting interested in something that, someday, someone else might find interesting, too?<

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