The compound is DSP-1181, from a collaboration between Sumitomo and the startup Exscientia (out of Dundee). It’s a long-acting 5-HT1a agonist, from what I can see (page 15 of that document). The coverage says that it “was created by using algorithms that sifted through potential compounds, checking them against a huge database of parameters”, and that this took one year to get into the clinic. If that’s accurate, that is indeed a fast path into human trials, but let’s look at what that might get you. Will this be a drug discovery revolution?
The problem is that preclinical drug optimization is not the problem. A more conventional program directed toward this mechanism might have taken two or three years to get to a clinical trial, and it’s important to realize that the idea of 5-HT1a as a target for anxiety and OCD is not a new idea. Here’s a review from 2009, for example. Exscientia has a good deal to say about its target-selection and compound-optimization technology, but in this case they’re going after a target that’s been out there for many years. The publicity for DSP-1181 emphasizes that it’s a long-half-life full agonist for the receptor (as opposed to some partial agonists that have been tried before).
There is indeed a long, long list of compounds with activity at 5-HT1a, and many of these have been in humans (or are already approved drugs with some 5-HT1a activity as part of their profile). The azapirones are a prominent example, although they certainly have other activities as well, and there’s 8-OH DPAT and Addyi (flibanserin) too. Outside of those multi-receptor compounds, there are some more selective ones such as befiradol (which is being studied for Parkinson’s), the related F-15,599 (being looked at in Rett syndrome), osemozotan (which has been into animal models of OCD and other conditions, but has not, as far as I know, advanced into human trials), repinotan (which was taken into the clinic for stroke, and failed), piclozotan (which appears to have also failed in a stroke trial), U-92,016-A, also billed as a long-acting full selective agonist, which has been around since the early 1990s and has not been developed, GPCR pharmacology is wildly complex, and nowhere more so than in the thick forest of serotonin receptor subtypes, so it’s certainly possible that a new compound could show a different profile. But it’s anyone’s guess as to what that profile might be. Just the list of different indications that such compounds are either used for or have been investigated for is enough to tell you what the field is like.
I have been unable to find a structure for DSP-1181 – patent applications from Exscientia are all directed towards machine learning techniques, and there is nothing I have found from Sumitomo/Dainippon on 5-HT1a. Although if that compound really is such new chemical matter, presumably a patent application hasn’t even published yet. When it does, or when the structure is revealed in a presentation, I will be very interested to see how closely it might resemble existing chemical matter.
Back the the mode of action. I used that word “guess” deliberately. For CNS drug discovery, that’s all we’ve got, AI or no AI. There is simply not enough reliable information to feed into even the greatest artificial intelligence software in the world to allow one to predict what will happen against conditions like OCD, depression, anxiety, and other high-level human psychiatric conditions. And that is the problem. Drugs fail in Phase II because we have not picked the right target, because our biochemical understanding of the disease state is wrong and/or incomplete. They also fail in Phase III for that reason and for unexpected toxicity, and the situation with tox is the same as for CNS efficacy: no amount of artificial intelligence is yet sufficient to tell you whether you’re going to run into such problems. Maybe eventually, but not yet. Those of you who remember Isaac Asimov’s “The Last Question” will recall the phrase “Insufficient data for a meaningful answer”, and that’s exactly the situation.
Here’s my take, then: Exscientia may well have moved a compound along at high speed into the clinic. But this particular example is not going to accelerate drug discovery much, because this is speeding up a minor part of the process and (for this target and indication) one that is nowhere near a rate-limiting step. We already have a whole range of 5-HT1a compounds, and we already have had (for many years) the idea that they might have applications in OCD. This project, at best, seems to me to have saved a few months off the process of sending their compound into the same black-box shredder as every such drug project goes into when it hits human trials. At this point, I believe they are now in the same situation as everyone else, which means a >90% chance of failure – honestly, CNS indications like this are more like 95%. AI has not changed that. I hope it does eventually. But it hasn’t yet.