So now I’ve been doing medicinal chemistry research in the drug industry for 20 years. That hardly seems possible, but since the evidence can’t be ignored, the next thing to do is ask: have I learned anything? What parts of my job am I good at? And, painful though it is to contemplate, are there things that I can’t do well at all?

Well, I’m still pretty good at bench chemistry, although I don’t do as much of it as I used to. Frankly, this is not a skill that’s valued as much as it used to be. As is well known, the less demanding chemistry is being shipped out to Shanghai and Hyderabad, and probably soon to even more exotic ports these days. My abilities to crank out libraries of amides and metal-catalyzed coupling products are either (at best) nearly irrelevant, and (at worst) dangerous. No one with a brain in their head would pay me my current salary to make libraries of amides. If I tried to make that a selling point for why I should be paid at that level, I would (and should) be brought quickly back to reality, perhaps by being ejected quickly through a real door.

No, if I were to make my bench skills any part of a keep-me-employed argument (still an inadvisable move, mind you), I’d want to emphasize the difficult things I can do that you can’t get in the overseas synthesis shops. But that brings up the next key point: all of the things that someone like me should bring to an organization should be the ones that can’t be bought cheaply, and that means that most of them have little to do with directly making compounds at all.

What didn’t come cheap was all that experience, and that’s where the long list of failed projects I’ve worked on comes into play. Like anyone else in this business, I’ve seen plenty of failures, and although many couldn’t have been foreseen, some were, in retrospect, rather more avoidable. And if I’ve learned any crucial lessons, these projects are probably where I learned them.

The difficulty is that you can draw the wrong conclusions if you’re not careful. You have to be honest about what could have been predicted and what couldn’t have been, and honest about what you knew about the risks at the time. Otherwise, you’ll hindsight yourself into believing that every program could have been figured out and every failure could have been avoided, and there’s just no reason to believe that that’s true. That line of thinking will have you drawing conclusions that can’t be safely drawn, and “learning” more than there actually is to know. But don’t go too far in the opposite direction, either, or you’ll end up rationalizing away every mistake as “just one of those things” that just happen, and that doesn’t help you learn anything, either.

So if I look back in that spirit, what avoidable mistakes come to mind? The first one is falling in love with in vitro potency. Or in vitro selectivity. Or in vitro anything, at the expense of going further and finding out the real answer in some kind of real animal (up to and including real humans). From what I can see, this happens all over the industry. Projects generate compounds that have all sorts of liabilities, but they’re just so wonderful in the screening cascade assays that no one can walk away from them. Admittedly, it takes a lot of nerve to stand up in some sort of project review meeting and say, “This is a single-digit nanomolar compound. It’s the most potent one we’ve got. And we’re not going to work on it any more.” But many are the drug discovery programs that have gone off the rails because no one said that while there was still time.

Another related mistake is to put off membrane penetration issues until it’s too late to really fix them. That could be oral absorption, or crossing the blood-brain barrier, or bacterial permeation. It’s hard to get away from transport issues, whether that means working your compound into some compartment, or watching it being pumped right back out. And here’s the problem: we don’t know much about how to fix these things. Basically, all we have are some guidelines for molecular weight, logP, polar groups and other such properties. Those are fine; they’re an appropriate thing to keep in mind when new analogs are being made. But if you’re already married to a compound (or a whole series of compounds) that have problems, then what are you supposed to do?

Well, too often the answer is something like “Uh, make a bunch more compounds in the class, and, well, kind of hope that we get lucky.” Of course, no one actually says it that way. No, you’re “addressing the PK issues through property modification,” or, “pursuing a more membrane-permeable scaffold.” As long as no one stands up in the back of the room and asks you how you’re really going to do that, you might be able to get away with that stuff. But to what end? What availeth it a project to make a long series of hot assay compounds that can’t do what they’re supposed to do, because they can’t get to where they’re supposed to go?

A final mistake isn’t one that’s specific to drug discovery – it’s more of a human psychology problem. That’s the sunk-cost issue: the tendency to keep on with an effort, even though it’s making no progress and has no clear path to making any, just because “we’ve come this far already”. That’s a terrible temptation, because it seems so rational. But it isn’t. Rationally, the time and work you’ve put into something is a done deal that nothing can affect. What matters is looking at the situation as it is right then, and figuring out if it’s tenable. Forget how much it’s cost so far, how much time it’s taken: if this project landed in front of you fresh, in exactly the shape it’s in, with all the work having been done by someone else, would you take it on or not?

It’s hard to do that, because by the time that sort of decision has to be made, the answer may well involve admitting that a good deal of effort has been spent on things that shouldn’t have been done. No one enjoys hearing about that, especially if they were supposed to be in charge of things while (in retrospect) the project wandered off into the weeds. Rather than face that atonal music, many project leaders have opted to slog on, hoping to redeem everything with a big win at the end. And hey, a big win at the end probably would redeem everything – but do you have a realistic plan that might deliver one, or are you (once again) hoping to get lucky? Perseverance is a virtue, but there are no unalloyed virtues.

So these are a few ways to waste both your time and the funds of others. There are more, but anyone who manages to avoid just these will have accomplished something rare.

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.