I’ve had a lot of people ask me about yesterday’s protein folding news as it relates to drug discovery. And while I did a post on that last year, I thought it might be useful to briefly lay out the real problems with drug discovery, as I see them. Most folks in drug discovery will find the next few paragraphs to be pretty obvious stuff, but that’s because we’ve been living it. Readers can decide for themselves, though, where improved protein folding predictions fit in.
One of our biggest difficulties is choosing the wrong target. No, really. We have all sorts of compounds that make it into human trials and then don’t actually work, because it turns out that our hypothesis about the underlying disease was just wrong. It’s hard to overemphasize this: we don’t know enough about human biology to make sure, much of the time, that we have grasped the right end of the stick. A few simple questions will illustrate the problem: what causes Alzheimer’s? What’s the best way to interrupt septic shock? What’s the underlying cause of Parkinson’s disease? What’s the best target to work on to deal with chronic pain? What’s the actual biochemical cause of major depression? If you wanted to reverse fibrosis in a given tissue, how would you best go about that?
You can do that sort of thing for quite a while. Some of these questions have slightly more plausible answers than others, but believe me, all of them will involve substantial risk as you go into Phase II trials in humans. Just look at the landscape around many of them – all the previous trials that have wiped out. So I think it’s fair to say that being able to do a better job of picking the actual disease-relevant targets for our drugs would be a great improvement. Unfortunately, there does not appear to be a general solution to this problem, since it involves a more detailed understanding of each individual disease.
Better models (animal and otherwise) of such diseases and conditions would be great to have, but that’s a high bar. The arguing over animal models of Alzheimer’s has been going on for decades, since the underlying difficulty is that humans are the only animal that actually gets Alzheimer’s. You might think that pain signaling would be a conserved process and that animal models would tell you a lot, but I have lost count of the number of compounds that work in such models but do not work in human trials, so there’s clearly something missing there. Model development in general sometimes runs into a chicken-and-egg question, since you would need to know a lot more about the disease before you can work up a good model to mimic it.
Here’s another: we would love to have a better warning system for toxicity in human trials as well. Many promising drugs have dropped out of the clinic due to unexpected tox effects, for sure – some of these turn out to be mechanism-related and some of them are just compound-related (where the compound does something else that you don’t want), but there are many instances where we can’t even make that distinction yet. Animal models for toxicity are extremely valuable, but they don’t get you all the way. You are still taking a risk every time a new compound or new mechanism goes into human trials, and it would be very useful if we could lower that risk a bit. The general solution would be some sort of system that exactly mimics human biology but doesn’t consist of a bunch of human swallowing pills. This is a difficult goal to realize.
To my mind, these are some of the biggest problems in coming up with new therapies. As a medicinal chemist, one of the things that you come to realize is that med-chem itself is often at the mercy of these things. You can deliver a potent, selective, bioavailable compound aimed directly at your disease target, only to find out in the clinic that whoops! That target doesn’t work. I have been involved in a good number of these over the years, and so has everyone else. No amount of compound optimization will fix that issue; the problem is bigger than the compounds.
So when you hear about a new technique that’s announced as speeding up the development of new drugs, ask yourself if it’s going to bear on the issues above or not. Now, that doesn’t mean that advances of that sort are useless, far from it. New techniques to screen compounds, or to find leads from the screening data, or to optimize them more efficiently into clinical candidates, new formulations and assays and delivery methods and mechanisms, all of that is useful. But all of those are upstream of the problems of target selection and unexpected toxicity. Finding out more quickly and with less expense that you have chosen the wrong target is no bad thing – but an even better thing would be to not choose the wrong target.