Underappreciated problems in AI for bio

So the world is suddenly investing in AI+bio. Every day a new splashy announcement comes out that a company has come out of stealth with a chunky $X00M dollar seed round and a $XB valuation. (Probably in milestone-gated chunks, but ssssh don’t mention that bit on Twitter.) Plus a lot of chatter around the ’neopharma’ concept, which I am unashamedly a fan of.

That said, in my experience the discourse pretty quickly devolves into just two talking points: (a) AI helps design drugs yaaaay and (b) clinical trials are still hard boooo.

As someone who’s been doing AI-for-pharma for a while (in addition to the neural ODE, JAX ecosystem etc. stuff that I think I’m better-known for in public), I wanted to add something a bit more detailed to the conversation. What are the underappreciated problems in AI+bio, the places where AI really stands to make a transformative impact? Even (or especially) when we keep in mind that yes, discovery is fairly cheap, trials are expensive, etc.

Here are four examples.

1. Assays at 10^2 scale

Find a way to measure any property of a protein at just 10^2 variants. This is the (surprisingly small) lower bound for optimizing that property with AI, fairly trivially, with about a 95% success rate. This is doable in just 3-4x 96-well plates. (I even know one place that consistently does just single-round optimization with reasonably high success rates.)

And like, also yes, you can raise $200M to build a fully-automated CRO and maybe that’s useful if you have a lot of customers who all need that 10^2-scale data, but just so we’re clear, any single customer wanting 10^6 has probably missed the memo.

This is a ‘meta problem’ that is likely solvable across a range of actual problems. The high cost of obtaining PBMC donors for immunogenicity assays, the cost of doing expression in GMP stable pools, etc. This is mostly a point about economics, not automation – though for some of these problems then automation may be the answer.

Disclosure: this particular optimization capability is specifically what’s available at Cradle, where I used to work. This is not the de-novo work you often hear about, which is still comparatively less-developed – as is commonly said, ‘a binder is not a therapeutic’.

2. “Neopharmas”

My Twitter timeline’s favourite topic over the past couple of days. Basically: point AI at making drugs, be better than is currently standard (along any one of twenty different metrics), declare success. Today there was the announcement that Prof Oak was acquired by Anthropic.

It’s kind of funny because this is very much a case of ‘what is old is new’. The virtual biotechs of yesteryear were sometimes ran out of a single person’s bedroom. A friend of a friend is single-handedly developing 3 ADCs through to preclinical efficacy. I know someone else who single-handedly oversaw 8 (!) drug programs through clinical trials (meshing together numerous CROs).

This historical context is underappreciated!

To be clear, I’m actually super bullish on the ’neopharma’ model, whatever that means. But I think it’s important to understand that ’neopharma’ is a class of companies – much like ‘software’ is a class of companies – and the VC pitch is the level of detail below.

3. NAMs, immunogenicity, and GLP-tox

A common refrain in regulatory policy circles these days is “NAMs” – “new approach methodologies” – for determining pre-clinical safety. Basically: right now we have almost no good way to determine is a drug is safe for humans… until we put it in humans.

We have some proxies (in silico estimates of MHC presentation using IEDB; tonsil-derived or organoid systems for measuring immune responses, or the use of cynomolgus monkeys), but these approaches are not predictive of safety in humans. Maybe we’re managing to screen out the worst candidates (maybe?) but for example there is no observed correlation between in vitro MAPPs assays and in vivo ADA rates.

The NAM thinking is that we need to find systems which are better models of humans: for example, more sophisticated organoid systems that better capture human biology, or AI tools trained to be predictive on (currently non-existent) human data. If there is a solution here, then I suspect it will require both new assays (to generate useful high-throughput data; also independently useful to start the flywheel) and new AI models.

4. GMP manufacture is the single slowest and most expensive line item on the path to the clinic

This will be a familiar refrain to any biotech VC in my audience: a startup is pitching you specifically to raise money for manufacture. Most of the raise will be going into that, in fact. And that kind of sucks for the VC because manufacture isn’t really a thing you’re underwriting a risk on, it’s just a huge sunk cost.

The cost of manufacture seems to be underappreciated by almost everyone I’ve spoken to in AI+bio. It is entirely possible to design a molecule for $500k, and for manufacture to take $10M. It’s uh, kind of a large line item.

There’s a lot of ways one could try slicing this Gordian knot: many of them are technical (e.g. some magic piece of cell line development that makes things faster/cheaper/whatever; alternate approaches to handling glycosylation; cell-free non-E. coli-derived GMP systems; etc.), some of is non-technical (e.g. changing regulatory conditions. For example on June 22nd the FDA announced that stable pools are now an acceptable choice for first-in-human studies.)

I think a lot of the interesting choices here will come from specialising on particular verticals: small-scale manufacture, particular kinds of therapeutic, etc., and in particular (at least for antibodies/proteins) to move beyond just CHO.

If AI+bio is going to have an impact on the life sciences, then we need to solve the capital constraint problem that manufacture imposes.

Summary

AI for biopharma is clearly going to have impact beyond the above – but for once I’d love to see the discussion move beyond the design of minibinders (now largely a solved problem) and the drafting of regulatory documents 😄