An AI-designed antibody binds: which decision comes next?

An AI model proposes an antibody. The molecule is produced and binds to its target in the laboratory. For a research team, that is meaningful progress. For company leadership, it opens another decision: which uncertainty has become smaller, and which investment is better justified as a result?

I approach this question as a physician and founder. Bringing AI into medicine requires explaining technical results across several levels. A convincing individual finding can change a research decision. Further questions arise along the path towards a treatment, each requiring its own evidence. Leaders who describe these levels clearly can make ambitious decisions while setting more precise expectations about what remains unresolved.

This reflection began with Joshua Meier and Matthew McPartlon's conversation with Sequoia Capital on 4 August 2026 about Chai Discovery. The founders describe molecular design as a route to faster experimental feedback. I develop a question of my own for pharmaceutical companies and investors: how should the choice of the next experiments change when more testable candidates become available? [1]

Define what a successful result establishes

The Chai-2 preprint posted on 6 July 2025 reports antibody fragments and nanobodies for 52 selected protein targets: hits for 26 targets and 15.5% binding hits among tested designs. It examines laboratory binding and identifies further characterisation needs, without demonstrating clinical efficacy. [2]

For an assessment, I would therefore ask for three separate statements: what was measured, under which conditions, and which next decision should follow? When a presentation moves directly from a laboratory observation to an expected treatment, part of the reasoning is missing. Making that part visible helps both sides of a funding conversation. Researchers receive a precise expectation; funders can see which uncertainty their money would actually address.

The unit of success should also remain clear. The proportion of designs that bind and the proportion of targets reached answer different questions. For a platform, breadth across targets may matter. For an individual development programme, the issue is whether a suitable candidate can be advanced for its particular target. Both perspectives are legitimate. A shared word such as “success” can easily obscure the different decisions behind them.

More options require a clearer selection rule

Consider a fictional research programme. A team can generate several candidates and has capacity for a limited additional investigation. One candidate binds especially strongly. A second leaves fewer questions about handling later in development. A third would test a different biological assumption. Which investigation comes first depends on which answer would most change the subsequent course of work.

My proposed selection rule is to record, before commissioning an experiment, which possible results would lead to which subsequent decisions. An investigation whose results would all lead to the same decision needs a different justification. It may be required for documentation or comparability. Its value in resolving a decision would nevertheless be limited. This distinction protects scarce laboratory time and makes the sequence of work easier to explain.

This is an organisational inference to be specified by the relevant specialists for each programme. It offers neither a general experimental protocol nor a shortcut through drug development. The responsible experts must determine which biological or technical uncertainty should be addressed first in the particular case. Company leadership can require that this connection be understandable without prescribing every experimental method itself.

Consider the properties together

In 2017, Jain and colleagues examined IgG1 variants reconstructed from 137 clinically advanced antibodies using twelve biophysical assays. The historical selection and standardised preparation limit transfer. These comparison data cannot reliably predict the success of a new candidate. [3]

What matters for my argument is the structure of the decision. Selecting a candidate means bringing several requirements together. An exceptionally good result may raise the question of how much additional work on other properties is acceptable. A scientifically interesting deviation may deserve investigation. That requires a reasoned comparison with alternatives and an understanding of the resources committed by the chosen path.

I would maintain this assessment as a short explanation that develops over time. It records why the candidate fits its intended purpose, which doubts remain and what would require the selection to be reconsidered. The original rationale then survives when a particularly striking new measurement captures attention. It also becomes easier to recognise when a previously plausible assumption can no longer support the decision.

Build collaboration around the handovers

For a partnership between an AI company and a pharmaceutical company, this creates a concrete design question: which result does one party deliver, and which investigation does the other undertake? The handover should clearly connect the candidate investigated, the model version used, the findings obtained and the questions still open. Missing evidence belongs in that account too. Otherwise, the receiving team may struggle to judge which assumptions it is accepting.

Feedback after the next experiment matters equally. When a candidate is set aside, the research team should learn which observation drove the decision and how confidently the cause can be assigned. Recording an unresolved cause as a definite model failure would be unhelpful, as would allowing a confirmed weakness to disappear from view. How such feedback may be used belongs in the agreement governing data and collaboration.

Investors can ask about these handovers without substituting for a specialist assessment. What additional knowledge should the next investment make possible? Which capacity is needed? What would a negative result change? The quality of the answer reveals how the company turns scientific uncertainty into a manageable programme of work. A growing number of designs provides a starting point for that planning.

Keep the clinical question in view

For physicians, eventual benefit to patients remains the reference point. It cannot yet be inferred from the early design stage. Understanding that stage is nevertheless useful: it influences which possibilities are pursued and how clearly their boundaries are communicated. An informed audience can recognise progress while identifying the work still ahead.

For the next conversation about AI in drug development, I therefore suggest drawing a shared map of how knowledge will accumulate. Alongside each convincing result, write the question it answers. Then add the next open question and the decision its resolution would enable. This gives technical progress a meaning that research teams, funders and future care providers can examine together.