About this Author
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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May 2, 2002

Anything Worth Doing. . .

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Posted by Derek

There are several types of questions in science. You could plot them on a graph, with axes labled "Important / Trivial," "Hard to Answer / Easy to Answer," to pick two useful distinctions. Note that those don't always correlate as well as you'd think. There have been profound scientific questions that turned out to be surprisingly easy to put to the test, once someone figured out the conceptual framework.

And, more controversially, there are problems that (as far as you can tell) aren't worth the effort it would take to work on them. That's what Peter Medawar meant when he advised working on hard problems, not necessarily just interesting ones. Almost any problem can be interesting, including a lot of trivial time-wasters. It's sorting those out that can be troublesome.

For one thing, sometimes things that look trivial turn out to be important. And science lives on incremental results, and by making connections between things that no one thought were related. But in many cases, you can restate the problem to show why something is worthwhile. Take Fleming and penicillin:

"This stuff landed on my petri dish and killed my bacteria - I'm going to find out what it is."
"Who cares? It's spoiled. Clean it out and get on with your work."
"But something killed off these bacteria, and it looks like this mold may have secreted it. Wouldn't that be useful, to have something that can kill bacteria?"

There's a lot more to the traditional tale of this discovery - we'll come back to that. But it illustrates the point that problems can often be presented in a way that shows why they're worth working on. Of course, you can take work that isn't worth doing and try to present it this way, too (look at some grant applications!), but you can usually spot the seams and stitches that had to be added.

And I can't deny that there have been important results that have been ignored when they first came out. But in most of those cases, they've been ignored because they weren't believed, nd they weren't believed because their (potential) importance wasn't in doubt.

I'm not suggesting that researchers shouldn't follow their own curiosity, or that we should have some sort of central review to tell us what's important and what isn't. You couldn't pay to advocate either of those positions; they're disastrous. But what I'm suggesting is that researchers should sharpen their own instincts, and put their curiosity to the best possible use. More on this as the week goes on.

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