Here’s a short review in ACS Medicinal Chemistry Letters on target validation. As the author (Ramzi Sweis of AbbVie) says, it’s easy for medicinal chemists to lose track of that being part of their role:
Too often, medicinal chemistry teams blindly accept the biological underpinnings of a new program as sound and are unaware that their ensuing efforts at compound optimization may confirm or debunk the link between the biological target and the disease. In many instances, this event occurs very early in the discovery process, at the level of preclinical interrogation.
The number of targets that you can be sure are good ones, before anyone’s actually made a drug to hit them, is not large. You rarely get signals like PCSK9, where you can point at a human population with exactly the phenotype you’re trying to cause (and even then, there’s always the worry that your therapy might not recapitulate that “human knockout” mutation in every respect). There are a few targets kicking around out there that have never really been “drugged” but that everyone’s still pretty sure would be great things to affect (p53 and/or cMyc in cancer, for example), but the list is short. Otherwise, unless someone else has already blazed that trail, you’re going to be finding out not only “Is this compound going to hit the target”, but “Is this target worth hitting in the first place”.
Here’s some good advice:
The infrastructure behind any drug discovery program should be stress-tested at a very early stage. Fear of obtaining suboptimal results from a suboptimal compound should not be a reason to defer such system testing. It is not uncommon for medicinal chemists to challenge their primary assay and note when occasional aberrations in output are observed. This feedback to biologists is quite helpful in establishing the durability of the primary assay. Accordingly, this philosophy should extend to downstream assays as well.
That fear is a very real one. “Oh, if you try to test using just the chemical matter we have now, you’ll probably kill the project for no good reason”. That’s not a silly argument; it really is possible to go in too early with something that’s too nonselective or too non-potent. But it can also be used to delay the day of reckoning, to avoid getting an answer that no one wants to get. You have to be honest with yourself and be ready to hear the bad news, and not keep telling yourself that you’re waiting for a better compound before asking the hard questions. Otherwise, you’ll have a compound that’s been optimized in every direction and is ready for the clinic before you know if you should have been doing all that work in the first place. Some readers may just possibly have had such an experience in their careers.
But as this paper goes on to say, even trying out your compound in vivo and seeing the effect you wanted may not be enough. That’s a big step, for sure, but you’ll be a lot more confident if you can hit the system with more than one chemical series. (This, in my experience, is a rare luxury). It’s a rare project that won’t charge ahead at this point (and a rare management team that won’t complain if they don’t).
The certainty of target validation/invalidation is far from absolute. It is akin to a lawyer’s task of establishing judgment beyond a reasonable doubt to a jury. A highly effective medicinal chemistry team is commonly lauded for intense focus. However, this focus should not preclude a critical assessment, from the broader perspective of drug discovery, of the compounds being used to make project go/no-go decisions. . .
If you don’t have that wonderful situation of multiple chemotypes, the paper suggests, then you should make the most of what you have – take some structurally similar compounds into the in vivo model, but ones that don’t have activity in the primary assay. These negative controls might surprise you. That’s also good advice, but can be a tough sell with some biologists. But from what I’ve seen, and from a look over the history of drug research in general, I’d say that skimping on the negative controls is both one of the most common shortcuts and one of the ones you’ll be most likely to wish you hadn’t taken.
Human nature is not built for scientific research. We have innate curiosity, no doubt about it, and we have pattern-recognition and narrative-forming abilities (and how). But what doesn’t come naturally is organized suspicion of our own convictions. That has to be learned, and relearned. In this line of work, the tuition can get expensive.