Here’s Robert Plenge at Merck, writing in Science Translational Medicine on what currently looks like the best way we have to do drug discovery. I’ll freely admit that I didn’t expect this article to be as good as it is (a lot of things with titles like this are crap). But he’s done a good job of laying out what you need to have the highest chances for success, and it’s good to have all of this summarized. He outlines four key features:
1. You need evidence from human biology before you even start. For infectious diseases, that’s pretty obvious, but for a lot of other targets, not so much. Careful study of human genetics and rare mutations can tell you a lot – if you have an idea for some protein as a disease target, it’s time to see if anyone has ever had the misfortune to be born with loss-of-function.Do not, Plenge warns, use animal models to pick or validate targets up front in the absence of evidence from humans beings or (at the very least) human tissues or cells. This requirement makes it very hard going in some disease areas, but that’s one of the points: those disease areas are going to be very hard to make progress in.
2. Your proposed target is going to have to be amenable to being modulated, and a lot of them aren’t. Gain-of-function on an enzyme, for example, is quite rare, unless you’ve got a bounce-shot inhibit-the-inhibition mode of action set up.Anyone interested in a gain-of-function protein-protein interaction target? You’d better not be. Targets that have no small molecule binding site at all are going to be a lot harder, too, naturally – you can think about an antibody in those cases, but you’re still going to be limited to what an antibody can do for you (which is basically to block a protein surface). All this ties back in to knowing the human biology: which knob you’re trying to turn and which direction you’re trying to turn it.
3. You need insight into biomarkers, and these need to be as human-relevant as possible. Some diseases have it easier here – diabetes, for example, But others are quite difficult, and you have to be careful not to be misled. Plenge says (accurately) that “Unfortunately, many pharmacodynamic biomarkers measure biological states that are irrelevant to human disease“, and you’d better not just end up measuring something because it’s the thing that you can measure. He also notes that epidemiology is a powerful tool, but by itself it says nothing about causality. Combining it with human genetic studies (“Nature’s randomized clinical trial”, as he puts it) gives you a much better shot at understanding what you should be looking for in blood or tissue during your own clinical trial, the one that you’re going to be paying for.
4. Finally, when you get to that trial, you need one that’s as small, fast, and meaningful as possible to test proof-of-concept. “Well, sure”, you’ll say, but taking this to its logical conclusion means that there are some diseases that you should strongly consider not even considering (see below). This also means that you need to be able to pick your patients very carefully to find the ones that are most likely to show a response (which ties in with the points above about already having connections to human biology). If you can do that, and if you have a real biomarker that you can trust, you’re in very good shape – well, as good as it gets in the clinic, anyway. The further away you get from these ideals, the more you’re rolling the dice.
OK, there are the principles. One of the good things about this paper, though, is that it honestly discusses the limitations of all these ideas:
First and foremost, there is an underlying assumption that we have sufficient data from humans to enable the discovery of new therapeutic targets and biomarkers. Validation of this assumption requires an ecosystem to define which sources of human data establish causality; members of the ecosystem must then work systematically toward building such databases that are accessible to all. For example, there is no single resource that enables systematic identification of human genetic variants linked to clinical outcomes in large patient populations (>10 million people) in a setting suitable for recall. Similarly, there is no large population with detailed molecular longitudinal profiling to identify novel biomarkers. It is encouraging, however, that many efforts are under way to generate these human databases.
Other problems include that you may not be able to get any decent “experiments of nature” by mining human genetic diversity, or even if you do, that they may well not tell you how much to modulate your proposed target. There’s also the problem that clinical trials technologies and designs may not (or not yet) allow for the sort of data collection and biomarkers that you’d like. Even with these complications, I’d say that these criteria are definitely worth aiming for. But even if you have all of them going for you, you can still easily fail in the clinic. Note also that even though many infectious diseases score high by these standards, targets for them can be hard to come by – those projects tend to have high preclinical failure rates, which aren’t addressed here.
One implication of these rules isn’t spelled out in the paper, but seems inescapable: this means that there are some diseases that you just don’t work on. Alzheimer’s is the first that comes to mind. The human biology of the disease is still a matter of intense debate; the potential targets likewise. And as for a short, high-powered proof of concept trial, well, we’re so far away from running one that it makes you want to weep. No, Alzheimer’s scores very high in the “unmet medical need” category, but you’ll note that that’s not one of the things that we’re scoring here. It’s up to you, in a separate exercise, to decide if a given disease or target is worth working on in that sense, but do note that huge medical need is totally orthogonal (at best) to any calculation of chances for success. Bernard Munos has said this for some time now: given the state of Alzheimer’s research, drug companies should probably abandon the field until we understand it better. That’s not going to be popular if you just come out and say it in so many words, but a number of companies have implicitly taken just that course of action by not working on the disease.
The biggest problem I can see with these rules is that it’s very, very hard to meet all of them at the same time. Something’s going to come up short, and judgment calls are going to have to be made about which of those are deal breakers and which aren’t. I’d say that lack of any human biology connection is a deal-breaker, for example, while lack of a really good fast-readout biomarker is just a sign that you’re going to be spending a lot more time and money in the clinic than you want to (not that that’s not a big consideration in itself). But I think that overall, Plenge is correct, that the closer you come to these ideals, the better off you’re going to be. They’re something to shoot for.