Having good ideas is hard enough, you’d think, since there never seems to be enough of them around. But I’ve come to realize that there’s more to discovery than good ideas. I have to admit, that’s not a lesson that’s come to me easily, and my position in the research world has made it even harder. Since I’m a medicinal chemist doing drug discovery, most of my work-related ideas are in that area. I don’t spend as much of my time thinking about the other parts of the drug development process, for one thing, and my ideas in those fields should be expected to have a lower success rate, anyway. I don’t know those areas as well as I know my own.

And that’s the big problem with any attempts I might make to improve R&D: the parts of it I know best are not usually the rate-limiting step. Take one of the tasks that I’ve had the longest experience in: making new compounds. Looking over the wider landscape of drug discovery, how will that improve things? Well, it won’t hurt, that’s for sure, unless I waste my time turning out toxic uglies, but they won’t let me or my lab do that for very long. So how much will it help?

As far as finding leads, well, drug companies have an awful lot of compounds to test already, and adding more of them to the pile will not necessarily make that much difference. Chemical space is very, very large, even if you take a pretty conservative view of what parts of it are likely to make useful drugs. A person could easily spend his whole life adding to it, and people have. To be honest about it, pointing to the sheer numbers of compounds you’ve made is like pointing at a particular pinch of sand on a beach.

The situation is better when you move to lead optimization and development, fortunately. We do need a continuous stream of new compounds for patent reasons, of course. And lead compounds always need work done on them to improve their profiles to where they can actually have a chance of making it. That sort of applied compound generation, the kind that’s trying to fix specific problems, is the heart of medicinal chemistry and probably the most valuable thing that we have to offer.

And although I spend a lot of time on that sort of thing, I still have plenty of blue-sky ideas about new classes of compounds to make, and some ideas about neat new ways to make them. And I plan to act on those – after all, I’d like to see if they work, and they could be useful. I’ll enjoy working on these things – I can already tell! – and who knows: the process of making them may go the way they’re supposed to. But that sand-on-the-beach aspect is what I don’t spend so much time thinking about: even if my ideas work as planned, they’re still overshadowed by the real problems that our industry has to deal with. And try as I might, I don’t think that medicinal chemistry (basic or applied) is the real answer to any of them.

These are not enjoyable thoughts. I’d like to believe that my best efforts in my own field are going to make a real difference, but I may be in the wrong part of the process to do that. The number of projects that fail due to problems with the medicinal chemistry is low – and low in price – compared to the ones that fail for more intractable reasons. You know the ones I mean – just look at where the money goes. The expense of all preclinical R&D is easily topped by the money spent on the first stages of the clinical trials, and that figure is overshadowed by the money that’s spent after that. Everything I’ve done in my career, in dollars and cents, is a roundoff error for a good-sized Phase III trial. If you want to change our world, find a way to avoid going through Phase III with compounds that fail, and find a way to get the compounds that succeed through more quickly.

Now that’s a tough set of problems, and there are billions of dollars waiting for anyone who would like to step up and solve them. The size of that unclaimed bounty is enough to demonstrate how difficult these goals really are. Reliable biomarkers, truly predictive toxicology, a better understanding of disease mechanisms in general: we’ve known for a long time that these are what we need, and no one’s been able to deliver yet.

But how much time does someone like me spend thinking about these things? If we discount the parts where I’m just sitting there going, “Man, I wish we had some of that,” then the answer is, “Not much.” But does that mean that the real answer is, “Not enough?” After all, if my own area is working comparatively well, shouldn’t I spare some thought for the ones that aren’t? Peter Medawar, the Nobel-winning immunologist, wrote about how scientists should work on the hardest problems that they possibly can. Any scientific problem, he pointed out, can be interesting, and take up all of your time. There’s no shortage of those; even essentially trivial stuff can be quite absorbing. But if something is going to take up your time, why not make it something with a bigger potential reward?

To be fair, it’s unlikely that I’m going to have any sudden brilliantinsights into (for example) predictive toxicology. But what I – and other chemists – can do is try to use what we know best in the service of that goal. A toxicologist I am not, but I can help come up with specific compounds to test new toxicology models, and I can apply my own chemical instincts to guide their selection. And I should also be willing to have some of my biases disproven by new evidence. There may well be structures and functional groups that I think are fine that are actually riskier than I know, and others that I’d throw away that may well be perfectly reasonable.

The same goes for general compound properties. There’s been a lot of argument about using simple screens and rules of thumb as filters. Some chemists complaining that these are unreasonable restrictions, and point at the number of exceptions to every rule that’s ever been proposed. I’ve done some of that myself, to be honest. But time and money really are limited in this business, and if I can improve my odds of making good compounds by even 10% by sticking within a certain property space, why shouldn’t I? Given the way this business works, that’s not an edge to give up lightly.

It involves swallowing some pride – but that wouldn’t do me (and many of us) any harm, either. Okay, okay: I can see enough people from the other departments nodding already . . . you folks do have enough to keep you occupied, right? I thought so. We all do.

Derek B. Lowe has been employed since 1989 in pharmaceutical drug discovery in several therapeutic areas. His blog, In the Pipeline, is an awfully good read.