Taking the fifty-thousand-foot-view of drug discovery and development is an unnerving exercise. A lot of people have gone up there in recent years, trying to figure out what’s going wrong and how to fix it. But what gets to me is what the exercise says about our problem-solving instincts.

As a medicinal chemist, my impulse (not surprisingly) is to come up with solutions that are med-chem-centric. It’s what I know best, so it’s what I’m most qualified to offer something useful in, right? I’ve spent most of my career in very early-stage drug discovery (rather than process, etc.), so my ideas are further biased toward that end of the process. But is that of any real use to anyone?
I say this because, to a good first approximation, I don’t think that medicinal chemistry is the rate-limiting step in the whole process, or the one most in need of fixing. (On the other hand, perhaps I’m just trying evade blame here, or shift it over to someone else!)

But think back on your own experience: how many programs have died, or cost the company significant amounts of time and money, because the chemistry kept coming up short? You may have a few examples, but I’ll bet that they’re overshadowed pretty easily by some larger problems. Those larger problems tend to cluster around the ruinous clinical trial failure rates in our business.
If you’re looking for something that would immediately make all of drug discovery more feasible, more useful, more profitable and attractive to investors, then just arrange it so that we fall on our faces a mere eight times out of ten rather than the current nine. That would double our drug output, and if that wouldn’t make everyone happy, I’d like to see what would.

And why do we fail? Numerous studies have gone over this ground, and the bulk of the wipeouts can be ascribed to lack of efficacy, or unexpectedly poor toxicity cancelling out what efficacy there was.

You know that already, and so do I. So why do I keep coming up with ideas that might make lead generation (for example) faster and easier? To use an organic synthesis analogy, I’ve come up with a way to break up the emulsion in the workup of step 4, while the big problem is that the crucial coupling at step 33 is still not working. The engine is hidden behind billowing clouds of greasy smoke, while I’m back there trying out new methods for wiping down the taillights and tightening the license plate holder. Thanks a lot!

Unfortunately, I don’t have a lot of good ideas about how to do predictive toxicology or anything to revolutionize the clinical biomarker field. I wish I did; I’d be out there shaking down investors right now and looking for office space, because those are some of the real problems. But they’re still the real problems because they’re really hard to solve, so I guess I should be glad to have what ideas I do.

What this means, though, is that in order to be worthwhile, ideas about areas such as lead generation need to be well-aimed. For example, you can pretty much always screen and get some sort of chemical matter for the well-trodden sorts of kinase, for example, so there’s really not much point in having some big insight that will help that process out. (By now, any such idea is, de facto, not all that brilliant – should have had it back around 1992 or so). But what if your new screening idea is applicable to, say, protein-protein interactions? Now there’s a tough field with a lot of interesting targets in it, and a new approach could open up a lot of new possibilities. Go to it!

The problem is, I think, that not many of us are big-picture sorts of people. The second problem is that a lot of the ones who actually are big-picture types are also not as grounded in reality as they should be. I remember a quote from someone saying that Woodrow Wilson had the most abstract mind that he’d ever encountered. A train would go by them, he said, and he’d see a train, whereas Woodrow would see Transportation. That’s not too helpful. But for the rest of us, being able to zoom out a bit would come in handy, as long as we don’t end up quite that far in the upper atmosphere. It’s a good mental exercise.

That said, where would a medicinal chemist’s imagination best be put to use? Thinking of ways to attack the tough targets, as mentioned above, would seem to be productive: new screening techniques, new kinds of chemical matter. Thinking of any methods in that area which are applicable across a wide range of projects and target types, rather than confined to one subset, is another. Fragment-based drug discovery, for example, can be applied all over the place—within its own constraints, it’s target- and therapeutic-area agnostic. Chemical biology can be very valuable by itself, and lead to a lot of valuable tools (and even potential drugs): we should be thinking about the interface between biomolecules and synthetic organic chemistry and trying to bridge the many gaps that have been there for too long already.

Inside medicinal and synthetic chemistry themselves, I’d suggest thinking of better ways to do the things we already know are valuable: fluorination for making things more metabolically stable, to pick one, alternatives to basic tertiary amines when you run into hERG channel and potential cardiovascular problems, good general ways to make compounds more soluble and easier to formulate (and good reactions to accomplish these things). We should always have our eyes open for new sorts of reactions that can be used to fill out structure-activity relationship (SAR) lists more easily. Palladium-catalyzed couplings are wonderful, for sure, but it would also be wonderful to be able to form bonds between nonaromatic carbons just as quickly and easily (a number of people are working on just that problem).

C. Northcote Parkinson, the British author behind “Parkinson’s Law” (work expands to fill the time available) had something to say about all this. One of his essays is set in a fictitious board meeting, where the only time everyone comes to life is when an issue is being discussed that’s trivial enough for all participants to understand completely. That’s the normal human tendency, but a lot of normal human tendencies will get you into trouble, as a brief study of history will make painfully clear. All of us, chemists, biologists, or what have you, should try to make sure that our own dialogue couldn’t be spliced too easily into Parkinson’s scene!