The big fashion in the last few years has been to detail the problems in the pharma industry. That fad started out inside the business, where those problems have been apparent for quite a while, and now it’s spread into the general press. We’re getting advice from everyone now – all the way from the New York Times to local op-ed writers, everyone wants to get into the act.

I should put “advice” in quotation marks, though, because most of these pieces spend much of their wordage just laying out the problems. And that’s useful, no doubt, for readers who are just coming to the story. Talking about the flat rates of new drug approvals (versus increased R&D spending), attrition rates in the clinic, regulatory hurdles, marketing costs, and patent cliffs is good for a surefire 1,200 words, although I just slammed through it in about 30. It’s in the last couple of paragraphs that these things tend to break down a little.

That’s where the writer is supposed to propose solutions. You can almost hear the gears grinding when it comes time to shift to that part of the article. With good reason, too, because that’s the hard part. Telling someone about their problems is always a lot simpler than telling them what to do about them, right? You’d think that the examples from within the trade press and scientific journals would do a better job at this point, but from what I’ve seen, they just get to the hand-waving section a little more quickly.

And hand-waving it is, for the most part. For example, I’d like for people to stop telling everyone that we have to reduce the failure rates in the clinic without offering any concrete ideas on just how to do that. Anyone can see that it’s something that would greatly help out the industry, and no one can see how things can go on with only 10% success – and increasingly expensive success at that. But honestly, if there were anything obvious to be done, it would have been done by now. There are billions of dollars waiting for anyone who can improve that process, which pretty much ensures that a lot of people have taken a lot of whacks at it. The fact that clinical attrition remains a problem is a good argument that it has no simple solution.

Not that anyone’s expecting one single magic wand to fix everything, true – but the dozens-of-incremental-improvements approach hasn’t been making any noticeable headway, either. Or perhaps it has, and those fixes have been getting canceled out (and more) by increasing problems in other parts of the process. At any rate, we didn’t get into this fix through just one factor going bad on us, so I’d be suspicious of anyone trying to sell One Dramatic Fix.

But if I had to pick one – listen for those grinding gears – I’d have to say that we have outsmarted ourselves, and have been in the process of doing so since (approximately) the mid-1980s. That’s conveniently just before I joined the industry, so take that timeline for what it’s worth. The culprit I blame is the entire shift to target-based drug discovery. In retrospect, many of those classic drug discovery stories – like the ACE inhibitors – may have contained within them the seeds of doom. Now, where exactly do I get off claiming that?

The lessons the industry learned from such successes, to my mind, were (1) that we need to pick good drug targets on the basis of biochemical pathways, (2) that the medicinal chemists could deliver once you gave them something like this to work on, and (3) that the key to success was to understand more and more about what you were doing. The truth, in other words, shall make you free. Sounds reasonable, and I have to say, I feel rather strange making a case against these propositions. But look at where they’ve gotten us.

Everything was fine, as long as we applied these techniques to the prefect targets to fit them. For example, angiotensin-converting enzyme and the angiotensin receptor itself are wonderful targets for hypertension. Face it, we’d chew on quartz to have such things these days: well-validated, tractable, highly relevant to a huge patient population. They just don’t make ’em like that any more, not as far as I can see. Many of the big successes from those days seem to fall into this bin, and I think that it gave us the wrong view of reality. We kept expecting that everything should be this clear, or that it would eventually become that clear, and it just hasn’t happened.

Applying the mindset of those cardiovascular targets to other therapeutic areas has led us off into the swamp. As complex as hypertension and lipid handling are, many of the other diseases are even worse, and less understood, to boot. The pathways are murkier, the animal models are less reliable, the clinical trials can be tougher. But we pressed ahead, thinking that if we just threw more molecular biology at the problem, more genomics, more proteomics, more biomarkers, things would start to clear up and we’d be back to working on solid ground again, banging away at solid targets that would make us some solid money. So now we’re in the position of Macbeth, stepped in so deep that “returning were as tedious as go o’er”. You don’t, I’d like to add, want to end up comparing your problems to those of Macbeth. But here we are.

So yes, when I say that we outsmarted ourselves, what I mean is that we convinced ourselves that we really did understand what was going on with these drug targets. If you were in a big company, it made you feel safer, like you were on more solid ground, and if you were in a small company, it was a great pitch for the investors. Even if we didn’t quite have all the dots connected, that was still OK, because we’d be filling in the gaps shortly, and it was fine to go ahead and start in on the drug development while the pieces settled down into place. Clarity was on the way. But it’s been on the way for quite a while now, and we’re going broke waiting for it.

My suggestion, then, is to get more humble. We should admit to ourselves – and to our customers and our investors – that we don’t understand what causes Alzheimer’s, that we don’t yet know what to do about most types of tumors, and so on. And while we’re continuing to try to puzzle those things out, we should be willing to go with anything that looks like it might work, whether we understand it well or not. That means phenotypic assays, better animal models, and going into the clinic more quickly to see what’s really happening. Embrace ignorance.

Now, it’s not like this is some golden road to clinical success. There isn’t one. (See above!) And it’s not like terrible mistakes can’t be made by this route, either. Bad phenotypic assays or bad animal models are worse than useless, andfiguring out which are the bad ones isn’t easy. But I think that we could do with more of this sort of thing than we’ve been trying for the last 20 years. Lining all the molecular biology and biochemistry factors up, then spending a few hundred million dollars a throw only to find out that we didn’t know as much as we thought . . . that hasn’t been working out so well, either.

Derek B. Lowe has been employed since 1989 in pharmaceutical drug discovery in several therapeutic areas. His blog, In the Pipeline, is located at http://www.corante.com/pipeline and is an awfully good read. He can be reached at [email protected].