My post the other day on why-do-it academic research has prompted quite a bit of comment, including this excerpt from an e-mail:
I would also note that mediocrity is hardly limited to academia. I cannot tell you the number of truly dumb things that I continue to see happening in industry, motivated by the need to be doing something - anything - that can be quantified in a report. The idea that industry is where reality takes command is depressingly false, and I would guess that the same thing that distinguishes the best from the rest in academia also applies in the "real world."
Well, my correspondent is unfortunately on target with that one. Industry is supposed to be where reality takes command, but too often it can be where wishful thinking gets funded with investor's cash. I'm coming up on my 20th anniversary of doing industrial drug discovery. I've seen a lot of good ideas and a lot of hard work done to develop them - but I've also seen decisions that were so stupid that they would absolutely frizz your hair. And I'm not talking stupid-in-hindsight, which is a roomy category we all have helped to fill up. No, these were head-in-hands performances while they were going on.
I can't go into great detail on these, as readers will appreciate, but I can extract some recurring themes. From what I've seen the worst decisions tend to come from some of these:
"We can't give up on this project now. Look at all the time and money we've put into it!" This is the sunk-cost fallacy, and it's a powerful temptation. Looking at how hard you've worked on something is, sadly, nearly irrelevant to deciding whether you should go on working on it. The key question is, what's it look like right now, compared to what else you could be doing?
"Look, I know this isn't the best molecule we've ever recommended to the clinic. But it's late in the year, and we need to make our goals." I think that everyone who's been in this business for a few years will recognize this one. It's a confusion of ends. Those numerical targets are set in an attempt to try to keep things moving, and increase the chance of delivering real drugs. That's the goal. But they quickly become ends in themselves, and there's where the trouble starts. People start making the numbers rather than making drugs.
"OK, this series of compounds has its problems. But how can you walk away from single-digit nanomolar activity?" This is another pervasive one. Too many discovery projects see their first job (not unreasonably) as getting a potent compound, and when they find one, it can be hard to get rid of it - even if it has all kinds of other liabilities. It takes a lot of nerve to get up in front of a project review meeting and say "Here's the series that lights up the in vitro assay like nothing else. And we're going to stop working on it, because it's wasting our time".
"Everyone else in the industry is getting on board with this. We've got to act now or be left behind." Sometimes these fears are real, and justified. But it's easy to get spooked in this business. Everyone else can start looking smarter than you are, particularly since you see your own discovery efforts from the inside, and can only see other ones through their presentations and patents. Everyone looks smart and competent after the story has been cleaned up for a paper or a poster. And while you do have to keep checking to make sure that you really are keeping up with the times, odds are that if you're smart enough to realize that you should be doing that, you're in reasonably good shape. The real losers, on the other hand, are convinced that they're doing great.
I'm not sure how many of these problems can be fixed, ours or the ones of academia, because both areas are stocked with humans. But that doesn't mean we can't do better than we're doing, and it certainly doesn't release us from an obligation to try.