We all know about target-based drug discovery. Enough biology has been learned that we think that Protein X is operating at a crucial stage in the development of Disease A, so we’re going to try to find an inhibitor/agonist/antagonist, a ligand/allosteric modulator/binder/potentiator, or something to somehow affect its actions. We’ve set up primary and secondary assays, we’ve got cellular and animal models ready to go, and now it’s time to test that hypothesis. I’ve spent a good part of my drug discovery career on projects that run pretty much like this, and I’ll bet that many industry readers have as well.
The problem is, of course, that you’re exposing yourself to several kinds of risk by doing things this way. The first is the risk that you may not be able to find any of those kinds of molecules that you’re looking for – at least, none that are good enough to turn into drugs. And the second is the risk that you do find one – and then you take it to the clinic and find out that well, raise my rent if it turns out not to be as important to the disease as we thought it was. Anyone who’s been around in preclinical drug discovery will have experienced both of these, from several different angles.
So then you have your phenotypic drug discovery. “We don’t know how these compounds work”, goes the oath, “at least not yet. But we do know that they do what we want them to do in a model system, and therefore we’re interested.” There’s a lot to be said of this, as long as you’re really, really happy with your model system (if you’re not, you’d better take that money and and make paper-maché sculptures out of it instead, because you’re going to lose it anyway, and you might as well have something to point at when you’re finished. You’d also better have the nerve to make the leap into human trials even if you don’t quite know how the compound works. Everyone tells themselves “Oh, no problem, we’ll do target ID by then”, but “target ID” is not a button that you pushthat tells you the target. It can be a multiyear effort that strains your chemical biology skills to the limit, and you have to decide if it’s worth going on with your drug candidate before it comes to a conclusion (if it ever does!)
This paper goes into detail on a third way of doing it, which is sort of located in between the other two. Target class discovery says “You know, here’s a bunch of proteins that all work sort of the same way and seem to be important. If we jump in, figure out something about them, and find some ligands, I’ll bet that something is bound to be a drug candidate for one disease or another”. I don’t mean for that to sound harsh – I think it’s a perfectly reasonable strategy if you weigh those various factors as well as you can. It’s not a new one, either. When you think about it, this is how many companies worked the kinase-inhibitor field back (say) fifteen years ago. If you cranked out a bunch of chemical matter with hinge-binding motifs and screened it, you found that you had a lot of compounds with inhibition profiles scattered around the “kinome”, and that led to the question of what to do with them. And if something showed up in the screens as weirdly selective for PQR kinase or what have you, the natural question was to ask if there were some disease where it really was a key player. It’s been a pretty useful strategy.
GSK did something like this starting in the mid-to-late 1990s with nuclear receptors, as this paper notes. That one, though, would have to get mixed reviews. Scientifically, it was unimpeachable: the company did a huge amount of work in the area, finding ligands, solving crystal structures, working out signaling behavior, and trying to understand the (hideously complex) biology of the target class. They weren’t alone – all the big companies (and many small ones) were working in the field after a while, and a lot of stuff got tried. But in the end, it certainly wasn’t as successful as the kinase efforts were. Two of the biggest nuclear receptor compounds, the PPAR-gamma ligands rosiglitazone and pioglitazone, were discovered before anyone knew what their targets were. And to the best of my knowledge, all the efforts to do other PPAR variations (and for other diseases besides type II diabetes) came to grief, and there were a lot of them (I contributed some myself). Other nuclear receptor types such as LXR, FCR, RXR and so on have also been the subject of a lot of work, but I feel pretty sure that if you gave someone in 2001 a look at the field in 2017, they’d wonder where all the drugs were.
It’s probably too early for this, but you might be able to say the same about another target class effort, the broad category of epigenetics. That may be unfair, because we’re not that far out of the initial hype zone with those, and there are a lot of stories that are still being written. But that target class, like the nuclear receptors, probably suffered (and suffers) from being too broadly defined, because there are several enzyme classes in there and some of them are considerably more likely to give you workable chemical matter than others. But they all share (like the nuclear receptors) a wildly complex biological back office. Going after gene expression with small molecules has tremendous potential and tremendous intellectual appeal, but these two methods of doing it still have a lot to be unraveled. Transcriptional regulation is gibberingly, rug-bitingly complicated, which is why there’s a real case for phenotypic work in the field: look for the effect you want and then figure out how the heck you got there.
If you’re going to go after a target class, you would do well to tailor a chemical library towards it, to the extent that you can. That’s what led to so much progress in the kinase world – the identification of chemical motifs that tended to hit the hinge region of those enzymes gave everyone a lot to work with. That’s about the best case, as the vast, massive patent landscape of kinase inhibitors will show. It’s usually a bit harder (and sometimes a lot harder) to figure out what kinds of chemical matter to invest time in making for the effort, but I’d say that it’s a key step in being successful. You can certainly screen the whole deck, and you probably should if you can, but you should also be ready work with whatever chemotypes turn up and make as big a party tray of them as possible.
You’re also going to need a really solid assay platform, preferably one that includes a lot of the target class members (with as much diversity as possible). Entering unknown chemical and biological territory with a severe assay bottleneck is very much not recommended; you need for the primary and secondary assays to generate the heaps of reliable data that you’re going to use to get your bearings. And as usual, if you’re going phenotypic, you’d better really love your phenotypic model, and be able to drive a lot of stuff through it.
As this paper points out, this sort of thing takes a long-term investment and a long-term mindset. Especially at first, progress is not going to be very fast, and people (especially Upper Management People) have to be ready for that. The idea is that as you get things worked out, you’ll get a platform together that will allow you to speed up and get some sort of virtuous circle of comprehension going. Ideally, you’ll end up with something that few or no competitors have, in terms of physical and intellectual resources, but that doesn’t come without risk. If you want to own a territory, you have to go out to the wilderness and stake a claim.