Bruce Booth has some thoughts here on a recent Harvard Business Review piece on startups, but don’t let the fact that it’s from HBR put you off from taking a look. The original article is focused on innovation in general, but Booth ties it more directly to biopharma culture, and his advice certainly looks sound to me. And it’s not just sound for people working in small companies, although they should definitely read it. The same lessons apply to doing R&D in any size organization.
I wanted to highlight one of those: the willingness to design and to run “killer experiments”. And by that I don’t mean in the “whoa dude, killer experimental design” sense, but rather in the “hard decision point” sense. Not every phase of one’s work lends itself to these things, but you will have opportunities to set up stuff that’s pretty close to pass/fail, and (here’s the hard part) you should not miss the opportunities to do so. Now, I’m not suggesting that you should wander around all the time trying to find excuses to kill your project. Every drug project has plenty of reasons why it can be killed. What I’m saying is to be alert to the chances to run definitive experiments that will put your hypotheses to a solid test.
Designing these experiments shouldn’t necessarily be easy – you’ll want to think hard about the best way to put things to the most direct test you can, with enough well-run controls that you’ll believe the result even if it’s bad news. That brings up something I’ve mentioned before, and that many readers will have experienced: sitting in a project meeting where a particular experiment is being proposed, and thinking that yes, if the results are positive, you’ll go on with the plan. But if the results are negative. . .well, you know, when you put it that way, you’ll go on with the plan anyway. At that point an alarm bell should go off to make you ask why you’re running the experiment anyway. It’s not that these are always useless, of course (sometimes you have to collect a value for some parameter, just to have it), but sometimes they are. The most insidious are the experiments that get billed as decision points when in reality they’re no such thing.
A real decision point experiment should make you nervous, frankly. You’re putting a lot on the line, and you should be committed to being ready to kill something off (some compound series, some approach, some assay, some hypothesis, maybe even some entire project) if things don’t go right. Don’t cheat. If you’re not going to follow through on what the experiment tells you as designed, redesign the darn thing to make it more convincing. Otherwise you’re just fooling yourself and/or trying to fool somebody else, and neither of those is an honorable or productive use of your time.
A corollary to all this is that such experiments should be run as early as it’s feasible to run them. The longer you wait, the more you risk (time, money, energy, and so on) and the worse will be the temptation to carry on no matter what. The normal tendency is to look for excuses, for reasons not to do this sort of thing, to fill in your busy schedule with all that other stuff instead of facing the music. Don’t. It’s bad enough that we work in a business where the killer experiments (clinical trials!) often have to take place after a great deal of time and money has been spent, but you don’t have to add to that in your own part of the process. Think about the most likely things would invalidate your work, and what the most solid, undodgeable bad news would look like. Then go make sure that it’s not there – do your best to conjure up those demons, because if you don’t do it now, you’ll be forced to do it later.
This is contrary to normal human psychology, but then again, the whole scientific method often seems to be contrary to normal human psychology.We’re wired more to fall in love with our own ideas and to pick and choose the evidence we will accept for and against them based on how it makes us feel. But that’s asking for disaster in science. We’re up against physical laws and phenomena that could not possibly be paying less heed to how we feel.
So put your ideas to the test. Take them up to the mountain and hold the knife over them. It’s the only way.