We talked a little while back here about "Lean Six Sigma" as applied to drug discovery organizations, and I notice that the AstraZeneca team is back with another paper on the subject. This one, also from Drug Discovery Today, at least doesn't have eleventeen co-authors. It also addresses the possibility that not everyone in the research labs might welcome the prospect of a business-theory-led revolution in the way that they work, and discusses potential pitfalls.
But I'm not going to discuss them here, at least not today. Because this reminds me of the post last week about the Novartis "Lab of the Future" project, and of plenty of other initiatives, proposals, alliances, projects, and ideas that are floating around this industry. Here's what they have in common: they're all distractions.
Look, no one can deny that this industry has some real problems. We're still making money, to be sure, but the future of our business model is very much in doubt. And those doubts come from both ends of the business - we're not sure that we're going to be able to get the prices that we've been counting on once we have something to sell, and we're not sure that we're going to have enough things to sell in the first place. (There, that summarized about two hundred op-ed pieces, some of them mine, in one sentence. Good thing that I'm not paid by the word for this blog.) These problems are quite real - we're not hallucinating here - and we're going to have to deal with them one way or another. Or they're going to deal with us, but good.
I just don't think that tweaking the way that we do things will be enough. We're not going to do it by laying out the labs differently, or putting different slogans up on the walls, or trying schemes that promise to make the chemists 7.03% more productive or reduce downtime in the screening group by 0.65 assays/month. This is usually where people trot out that line about rearranging deck chairs on the Titanic, but the difference is, we don't have to sink. The longer things go on, though, the more I worry that incremental improvements aren't going to bail us out.
This is a bit of a reversal for me. I've said for several years that the low success rates in the industry mean that we don't necessarily have to make some huge advance. After all, if we made it up to just 80% failure in the clinic, that would double the number of drugs reaching the market. That's still true - but the problem is, I don't see any signs of that happening. If success rates are improving anywhere, up and down the whole process from target selection to Phase III, it's sure not obvious from the data we have.
What worries me is that the time spent on less disruptive (but more bearable) solutions may be taking away from the time that needs to be spent on the bigger changes. I mean, honestly, raise your hands: who out there thinks that "Lean Six Sigma" is the answer to the drug industry's woes? Right. Not even all the consultants selling this stuff could get that one out with a straight face. "But it'll help!" comes the cry, "and it's better than doing nothing!". Well, in the short term, that may be true, although I'm not sure if there is a "short term" with some of these things. If it gives managers and investors the illusion that things are really being fixed, though, and if it takes mental and physical resources away from fixing them, then it's actually harmful.
What would it take to really fix things? Everyone knows - really, everyone does. Some combination of progress on the following questions would do just fine:
1. A clear-eyed look at target-based drug design, by which I mean, whether we should be doing it at all. More and more, I worry that it's been a terrible detour for the whole project of pharmaceutical research. There have been successes, of course, but man, look at the failures. And the number of tractable targets (never high) is lower than ever, as far as I can tell. If we're going to do it, though, we need. . .
2. The ability to work on harder target classes. The good ol' GPCRs and the easy-to-inhibit enzyme classes are still out there, and still have life in them, but the good ideas are getting thinner. But there are plenty of tougher mechanisms (chief among them protein-protein interactions) that have a lot of ideas running around looking for believable chemical matter. Making some across-the-board progress in those areas would be a huge help, but it would avail us not without. . .
3. Better selection of targets. Too many compounds fail in the clinic because of efficacy, which means that we didn't know enough about the biology going in. Most of our models of disease have severe limitations, and in many cases, we don't even know what some of those limitations are until we step into them. Maybe we can't know enough in many cases, so we need. . .
4. More meaningful clinical trials. And by that I mean, "for a given cost", because these multi-thousand-people multi-year things, which you need for areas like cardiovascular, Alzheimer's, osteoporosis, and so on, are killing us. We've got a terrible combination of huge potential markets in areas where we hardly know what we're doing. And that leads to gigantic, expensive failures. Could they somehow be less expensive? One way would be. . .
5. A better - and that means earlier - handle on human tox. I don't know how to do this one, either, but there are billions of dollars waiting for you if you can. Efficacy is the big killer in the late clinic these days, but that and toxicity put together account for a solid majority of the failures all the way through. (The rest are things like "Oops, maybe we should sell this program off" kinds of decisions).
There are plenty of others, but I think that improvements in those would fix things up just fine. Don't you? And maybe I'm just slow-witted, but I can't see how changing the way the desks face, or swapping out all the business cards for new titles, or realigning the therapeutic area teams - again - are going to accomplish any of it. At best, these things will make the current process run a bit better, which might buy us some more time before we have to confront the big stuff anyway. At worst, they'll accomplish nothing at all, but just give the illusion that something's being done.
To be fair, there are some initiatives around the industry that address these (and the other) huge problems. As I said, it's not like no one knows what they are. And to be fair, these really are difficult things to fix. Saying that you want to get a better early read on human tox in the clinic, the way I just did so blithely, is easy - actually doing something about it, or even finding a good place to start doing something about it, is brutally hard. But it's not going to be as brutal as what's been happening to us the last few years, or what's we're headed for if we don't get cracking.