It seems to be a fairly slow news day in biopharma – not always such a bad thing – so I wanted to bring up a general drug discovery question. Unfortunately, I’m not sure it has a good answer. What is the proper balance between perseverance and pragmatism – in other words, how do you know when to give up on a given compound, series, or project?
That’s akin to the “when do you sell a stock” problem, and right off, it’s important to note that there are big mistakes to be made in either direction on any question like this. The Sunk Cost Fallacy is waiting to tell you to hold on too long, that you’ve come this far and that now is no time to quit, no matter how horrendous the situation may have gotten. Interestingly no phrase comes to mind that describes the opposite error, that of bailing out too quickly, but that’s certainly a real phenomenon as well. It’s for sure that if you don’t have a fair amount of grit and determination that you’re never going to get a drug project to work, but it’s also for sure that grit and determination by themselves are just not enough – necessary, but not sufficient, to use a favorite phrase.
There are social and psychological components to this as well. People tend to admire fortitude and staying power, and you can bring on a whole list of football coach sayings as evidence: “A winner never quits, and a quitter never wins”, etc. Even historically, people know the names of more battles and generals where a heroic (and doomed) last stand was made compared to the examples where someone actually managed to save themselves and their army to fight (and win) another day. Not long ago, I was re-reading Ron Rosenbaum’s article about 1960s and 70s nuclear strategy in his collection The Secret Parts of Fortune, and came across the part where he described how studying surrender strategies had been a career-ender for people in the field. We really don’t want to hear about giving up.
Perhaps that’s because we worry that giving up might become too much of a habit. It is easier, for sure, and that’s the problem. As mentioned, any drug discovery project is going to go through patches where things look bleak, and if you drop one every time that happens, pretty soon you won’t have much left to drop. So running for cover every time is bad, and holding on to every possible bitter end is bad – how do you steer between these two ditches and stay on the road?
The best advice I have is to think really hard before you start and try to set the most realistic goals and milestones you can. “If by (date) we haven’t been able to (goal), then we need to rethink” is how these should probably look. “Rethink” doesn’t mean “abandon the whole thing”, either – it just means that you need to stop and take a look around, see if there really are believable ways out of the situation and how much they’ll cost you compared to the eventual goal. “Eventual” is a key word there, because it’s easy to get caught up in thinking that the goal is to keep the project going, one way or another, or that it’s to make the screening cascade as beautiful as possible, or whatever. No, the goal is to deliver a drug candidate, better yet, a drug. And it doesn’t have to be the drug that you’re working on, either, if the time, money, and resources that are being spent on the project at hand might be better spent somewhere else.
Be honest, then, about what can should be accomplished by when. That way, if you’ve done it, you can feel more confident that things are moving in the right direction. And if you haven’t, then you know that the time to take stock has come, and not to put it off in the hope that things will just somehow get better. If various things have turned out to be harder than they looked, fine – happens all the time. You just have to make sure that their difficulty hasn’t gotten to the point where calling a halt makes sense.
That’s because calling a halt does, in fact, make sense sometimes. The best way to do it is with a hard endpoint: here’s a model or an assay we trust, and if our best compound can’t show the right effect in it, we must be done, unless we can come up with a damn good reason why that happened and a clear plan to get around it. Not every compound is going to work, not every compound series can be developed, not every target is druggable, and not every target is even a good idea to go after in the first place. Our failure rates in the clinic are a big, steaming, pile of evidence for those statements. It’s tempting to think that we’d be in much better shape if we shouldn’ta hadn’ta worked on some of them at all.
But back to the opposite error we can go. The “fail fast” idea has been around for years now for that very reason, and it’s easy to understand its appeal. The expenses just get worse and worse as a project goes forward, and if you could just avoid going down some of those roads. . .the problem is, though, that if you’re going to Fail Fast, you need to be as sure as possible that you’re failing for the right reasons, and assays that are that trustworthy are not easy to find. People have messing things up by being so focused on being able to make the call that they pick an assay that isn’t so great and treat it like an oracle. That isn’t going to end well, but having no game-deciding assay at all won’t end well, either. Think, for example, of a phenotypic project. If you haven’t found the mechanism for your active compound, you’re going to have to make a big leap of faith into the clinic based on the results from your animal assay (or whatever the phenotypic driver was). But what if you don’t know if you can trust that assay? (“Then you shouldn’t have started the phenotypic project” is one response, but it might be too late for that to do anyone much good). How do you fail quickly and cleanly in a situation like that one?
In the end, many people will end up making decisions based on what’s worked (or not worked) for them in the past. And while experience is clearly valuable, it can hose you down, too. People who have been burned by letting projects go on too long will be more susceptible to killing future ones off too early, and people who feel like they were robbed of a project that actually was going to work will be more likely to let things drag on. “They fill you with the faults they had”, as Philip Larkin famously said about parents and children, and experience does it to us in other ways as well. All of us are guilty, at one time or another, of thinking that we know more about what we’re doing than we really do. That can hit you early in your career if you haven’t grasped the extent of your ignorance yet, and it can hit you later on if you think that you’re past that stuff (you aren’t – ignorance is a large subject and has plenty of room for us all). Perhaps one of the things that experience can (or should) do for us is remind us that experience itself is of limited applicability.