So, I do a post where I wonder if the reductionist target-driven approach to drug discovery is running out of gas, then I do one on the possibility of some interesting new drug targets in the brain. Am I deliberately talking out of both sides of my mouth, or do I just not remember what I've written the day before?
Actually, I can hold both of those views simultaneously. Order now and I'll send you my exciting at-home kit which will allow you to do the same! Here's how it's done: the morphine-synthesizing enzymes in brain cells that I spoke about yesterday are, indeed, possible drug targets. But I'm defining "target" pretty loosely here, as "theoretical possibility for therapeutic intervention." The step beyond that is "validated target", and we're a long way from that.
The problem is, no one has the faintest idea what brain cells are up to when they make morphine. I should start out by saying that we don't know which brain cells, of the insane number of different types, actually make it in vivo, what parts of the brain they're located in, or what factors cause them to increase or decrease its production. And once it's made, we don't know what it does or why. Presumably it's binding to the known opioid receptors, whose biology was complicated enough already, thanks. (See this recent paper, pointed out in a comment to the last post.) But there are already families of endogenous peptides that do that, so you have to wonder why morphine is in there, too. Under physiological conditions, perhaps there are other signaling roles for it (intracellular ones, maybe?) of which we are entirely ignorant.
But it's fair to assume that it's in there for a reason, and it's also fair to assume that disrupting its production would have an effect, even if we don't know that that might be. That makes endogenous morphine production a potential target, and an interesting one. But if we wait until these questions are well worked out, we could be in for a long wait. That's been the problem with many molecular-level targets, and Monday's post spoke about some of the difficulties with them.
How do you get more information? One way to approach the problem would be to disrupt one of the key enzymes used in endogenous morphine synthesis, once we know what they are, and see what happens. You could do that with RNA interference in cell cultures, but it can be hard to see what the effects are unless you touch on something vital. That's especially true with CNS targets, because cells in a dish are an extremely poor surrogate for the complex properties of the intact brain. A better route would be to go into whole animals: you could knock out the enzyme in mice and see how they develop, but the big question with knockout animals is how they compensate during development for that induced loss of function. Sometimes the changes you bring on end up being too subtle to catch, and you get what looks just like a normal mouse.
You'd probably be better off with a small-molecule enzyme inhibitor which could be dosed in a normal adult animal. If it's selective and nontoxic enough, you'd have a chance to see what the loss of endogenous morphine does under real-world conditions - assuming that it's something that can be noticed at all in an animal model, and assuming that you're sharp-eyed enough to catch it. Does it affect motor control, memory, emotional state, sensory input, or what? If you give it to a rat and he goes off and flops down, is that because he's dizzy, because his legs don't feel right, because he feels sick to his stomach, because he's suddenly sleepy, or because he's overcome with waves of rodent ennui? You can untangle some of those, but it isn't easy. You'd know, though, that it certainly does something, even if you're not quite sure what it is.
So, your choices are: go with the molecular approach, but be prepared to wait years for answers. (Be prepared to wait decades if the answer ends up requiring a molecular-level understanding of something like long-term memory or emotional state.) Or, go with the whole-animal approach once you've got some idea of the target, but be prepared to see no changes, or changes that you're unable to interpret or extrapolate to humans.
What I'd do, were I in charge of such an effort, is give the molecular approach some time at the beginning to see if they could narrow things down a bit. Is morphine made only in the brain, or also in the peripheral nervous system or also in other tissues entirely? What regions of the brain look most important? What enzyme should we be targeting to best affect the whole system? These could take a while, but not as long as working out the whole story would. Once we had some idea about the enzyme, I'd turn around and screen against it, looking for some chemical matter to try animal studies with. Getting something suitable might be a matter of months, or it might be a matter of years. How much time and money were you thinking about spending? This would be a major effort, clearly, and one unlikely to take place inside one research organization, no matter how dedicated and well-funded.
But here's the problem: this target, compared to some of the things that came spilling out during the genomics craze, is actually pretty well-grounded. Think about it - we have receptors that we know will bind morphine, and a lot is known about their biology (even if we don't understand what morphine is doing in there with them in vivo.) We're pretty sure that this will be a CNS target, rather than, say, cancer or diabetes (although I'd never say never until I saw more data.) We even know what kind of enzymes to search for in the morphine biosynthesis pathway, based on what we know from plants.
No, although I've just spent all this time talking about how hard it would be, this project would have a real head start compared to many of the things out there. And if you find that a bit unnerving, then you can see why the strict molecular from-the-bottom-up approach is running into problems.