Executive Summary

Key Figures

Source: Edwards et al., Biology-in-the-loop: Amortized Adaptive Hit Discovery in CRISPR Screens, arXiv:2609.11877 (2026), Table 1 and Appendix B

A screen in this paper is defined by three things: a natural-language description of the experimental setup, the list of genes measured in that experiment, and a binary label on each of those genes. A gene is a hit or it is not. The policy picks 100 genes out of that library and hands them over, gets the labels for those 100 back, and chooses the next 100 in light of what came back. Ten of those round trips exhaust the budget. The genes picked add up to 1,000.

All 20 test screens are genome-wide, with 18,000 to 22,000 genes in the library. Against a library that size, 1,000 genes come to a little over 5%. Two more conditions applied: at least 50 hits, and a hit rate no higher than 15%. Both keep out screens that are too easy and screens with no signal in them. Training screens all date from before 2021 and test screens from after, so the split runs along time. Comparing the hit set of each test screen against the training side gives a median Jaccard similarity of 0.064.

One more condition applies, and it changes how the headline number reads. A screen could enter the test set only if a language model reading nothing but the screen description picked up a minimal signal. The filter kept screens where the best-performing language model from the earlier benchmark scored at least 0.05 on a ranking measure over its top 100 picks. Because of that floor, the appendix states outright that AssayBench-Loop is not an unbiased sample of all genome-wide CRISPR screens. The set was assembled to measure adaptive discovery on screens whose descriptions really do carry predictable signal. The 27.7% is an average over those 20.

The primary metric, enrichment factor (EF), divides the hits found by the hits a random pick would be expected to find. The denominator carries one adjustment. When a model returns a gene name that does not exist, or fails to fill a batch, that share stays in the denominator as a penalty. A pick that names a real gene which the screen simply never measured draws no penalty, since a retrospective record is no ground for calling it wrong.

On this scale random selection lands at EF 1.04 and recovers 4.9% of hits. The value belongs near 1 by construction, and there it came out. The trained policy's 5.67 and 27.7% come from the same conditions and the same average over those 20 screens.

The model never sees a gene sequence. Its input is one block of screen description plus the genes tried so far and the results they returned. AssayBench-Loop, the benchmark built for this work, holds 1,389 screens: 1,349 from before 2021 for training, 20 from 2021 for validation, and 20 from after that for testing. All three sit on AssayBench, an earlier public benchmark of 1,920 screens, and inherit its temporal split.

AssayFormer, the policy model, is small: a three-layer transformer encoder, two attention heads, width 384, feed-forward dimension 1,024. Order carries no meaning among the input tokens, so it has no positional embeddings either. Each gene's token concatenates that gene's embedding with an embedding of its binary label. Whether the gene came back a hit enters the model with the same weight as which gene it was.

The starting point of those gene embeddings is the sore spot of this paper. The team spread every training screen into a gene-by-screen binary hit matrix, split it with Bayesian probabilistic matrix factorization, and used the result as the initial values. Those values carry one thing only: which genes came up as hits together in the same screen.

Supervised training goes on top of that, and reinforcement learning (GRPO) finishes the job. One device sits inside the reward. The number of hits a policy with no view of the history would have found in the same round is subtracted first, and only the difference is paid out as reward. Hits available without any context earn nothing. The paper calls this the context-delta reward.

An ablation confirms that the device earns its place. Training against the enrichment factor at the end of the tenth round instead brings EF down to 4.29, which sits 0.54 below the 4.83 obtained with the context-delta reward. A reward paid on the whole haul leaves a fainter signal for learning to move with the history, and that is the argument behind the design. The same table holds a condition that strips out the screen description altogether. With the natural-language text erased and only the history left, EF is 4.52. The record of what was perturbed and what came back, rather than the sentence stating the purpose of the experiment, is the main fuel for this model.

A large language model holds one seat in this loop. For the first three rounds the language model reads the screen description and proposes candidates, and from the fourth round the trained policy takes over. The validation set decided how many rounds to leave to the model, and k=3 came out. Early on no results have accumulated for a learned policy to lean on, while later the language model stalls first as results pile up. The two stitched together go by the name AssayLoop.

Beating random selection by 5.67 times tells a reader very little on its own. Adaptive design methods were already in use in this field, and the comparison worth making sits there. Pulling the main methods out of Table 1 in the paper shows distinct tiers.

The methods that take their bearings only from results returned inside the screen in progress, without reaching for past screens, cluster at LLMNN 2.39, Probability-of-hit 2.41, BioBO 2.59 and ICBR-EF 2.76. Screen-kNN, which does pull in past screens, sits at 3.40, MAML at 3.77 and BPMF at 4.49. None of those three were built for adaptive hit discovery, and drawing on past data alone lifted them into the upper tier. The paper cites that contrast as the motivation behind AssayFormer.

How handing over past data differs from training a policy on it shows up in one row of the table. That row reports a general-purpose coding agent with direct access to the training screens, run on the same budget. Claude Haiku 4.5 used straight as the acquisition policy reaches EF 1.39, barely clear of random selection at 1.04. Wrapped in an agent that can search the archive itself, the same model climbs to 3.20. Even so it never reaches the 4.83 of an AssayFormer trained on that same data.

Standalone language models also score fairly high, 4.7 to 4.8. Whether that score comes from prior knowledge or from the results returned each round is a question this field had answered both ways. One earlier study reported that the performance of experiment-design agents barely responded to feedback received during the experiment, and another reported that a good enough model gains a great deal from that feedback. The team measured the question again by deleting the outcome labels alone and leaving the list of chosen genes in place. Every language model tested performed worse. The result lends weight to the side holding that these models read the feedback and act on it.

The drop is not large, though. Gemini moved from 4.71 to 4.38, and GLM 5.1 from 4.00 to 3.65. A trained policy gains far more from the same history. On the job of reading results and changing direction, a policy trained explicitly for that still does better, and the paper leaves the matter there. The design that hands only the first three rounds to a language model came out of this contrast.

If the hits came that cheaply only because they were obvious ones, the story changes. The paper measures the share of DepMap common essential genes among the recovered hits. Knock one of those out in any cell and the cell dies, which makes them easy hits in screen after screen. The baseline that simply re-picks hits which recurred often in the past had that share at 99.1%. AssayLoop sits at 30.1% and AssayFormer alone at 40.7%. Random selection is 18.6%, so the record is hardly spotless, yet it is a long way from copying an old answer key.

A policy could also raise its hit count by working a narrow patch of biology, so the paper measures the breadth of pathways touched. At the dataset scope the effective number of pathways is 70.4 for AssayLoop, 66.2 for Gemini alone and 65.0 for AssayFormer alone. The widest of all is random selection at 82.6. Saying the policy raised hits without narrowing the search holds up. Saying it swept the widest does not.

This measure is taken at three scopes, and a note under the table warns against comparing across them. At the scope of a single screen the order shifts. The screen-level count is 34.6 for Gemini alone against 46.7 for AssayFormer alone and 50.7 for BPMF. A language model touches different biology in each screen, which looks broad across the whole dataset, while inside any one screen it sweeps a narrow neighborhood. The paper reads that as a property fit for an early warm start and short of what carrying many rounds demands. AssayLoop holds 46.6 at the screen scope, keeping nearly all of AssayFormer's breadth while lifting EF from 4.83 to 5.67.

The same principle carries over into a language model as well. Traces of the acquisitions GLM 5.1 left behind served as supervised training data for a 27-billion-parameter Qwen 3.6, with reinforcement learning added after. EF climbed from 2.65 to 3.56 and then to 3.69, a 39% improvement. Here too the training material was the order of choices another policy had left behind.

Calling experimental history an asset requires two things on the record. More history has to bring better results, and that history must not be replaceable by knowledge available elsewhere. The paper answers each question with an experiment.

Quantity comes first. The team trained 216 separate models while growing the training pool from a single screen up to 1,349. Performance rose monotonically across the whole range, with no sign of bending even at the largest dataset. EF more than doubled over that range. The ablation in the same section cuts deeper. A nearly 40-fold stretch in model parameters brought almost no gain. The authors conclude that in this regime the number of past screens in hand, rather than model size, sets the ceiling.

Replaceability comes second. The same training was repeated with seven different starting points for the gene embeddings: a random initialization carrying no information at all, GenePT embeddings built by running gene description text through a language model, representations taken from Perturb-seq experiments in the K562 cell line, and four factorizations of the training hit matrix. The spread of the results is wide.

The two starting points carrying biological knowledge sit at the bottom. GenePT in particular came in at EF 1.06 after supervised training alone, barely distinguishable from picking genes at random, and reinforcement learning brought it up to 2.60 without ever passing the 2.71 of an initialization that started from no information whatsoever. The four starting points drawn from the training hit matrix all land in the fours.

How the same material gets factorized also parts ways at the finish. After supervised training alone SVD sits at 3.72, close on BPMF's 3.83. Reinforcement learning pulls them apart to 4.40 and 4.83. That stage lifts all seven starting points, and in doing so it widens rather than closes the gap between BPMF and the rest. The largest climb belongs to GenePT, which moved from 1.06 to 2.60. It rose the furthest and still finished lowest.

In the appendix the team measured how well each embedding recovers the gene relationships recorded in standard databases such as STRING, CORUM, SIGNOR and Reactome. Embeddings that hold textbook relationships well turned out to be harder to train on this task, a negative relationship. The BPMF embeddings organize themselves around the phenotype of the screens where genes appeared together, rather than around pathways or complexes. That geometry barely moves during training, at a correlation of 0.999. AssayFormer learns on top of this structure rather than reshaping it, as the paper reads the result.

To look directly at what the policy learned, the team adds a single gene to the history as a hit and measures which way, and how far, the acquisition score of another gene moves. Fifty randomly drawn genes served as the background history, resampled ten times and averaged. Across a panel of 31 genes, 12 canonical cancer drivers and 19 drawn from functional modules, one property stands out. The relationships are not symmetric. The correlation between the influence matrix and its transpose comes to only 0.16, and 44% of reciprocal pairs carry opposite signs. Observing MDM2 as a hit raises the score of PFDN4 by 0.33, while observing PFDN4 lowers the score of MDM2 by 0.46. A table recording nothing but how similar genes are to one another yields no such direction.

Removing every pair already annotated in STRING, CORUM, SIGNOR, MSigDB and Reactome and taking the largest remaining influences, observing MYC as a hit raises the rank of SMU1 and PRPF4. That direction agrees with existing reports on oncogenic MYC and its dependence on spliceosome machinery. MDM2 is followed by EMG1 and PNO1, which connects to the surveillance pathway where disrupting small-subunit ribosome biogenesis stabilizes p53. Three pairs turned up whose influence grows sharply in one screen alone, a mark of the same policy behaving differently by context. The authors state flatly, though, that these values are decision rules the model uses internally rather than established biological interactions. Nominating candidates for later validation is as far as this analysis goes.

The next experiment asks whether the learning amounts to plain memorization. One of the five phenotype categories is withheld from training entirely, and the model is evaluated on screens belonging to the category that was left out. Gathering the full test set this way gives EF 4.59, not far from the 4.83 obtained with all five categories in place. Screen-kNN falls 0.42 under the same condition while AssayFormer falls only 0.24, and an AssayFormer that learned without one category still stands above a Screen-kNN that saw them all.

The amount of data removed differs greatly by category. Of the 1,349 training screens, the fitness, proliferation and viability category accounts for 947, while the trafficking, localization and structural category holds 38. Withholding one cannot be a test of the same weight as withholding the other. The authors accordingly limit this experiment to a robustness check against category exclusion, and warn in the body against reading it as a proof of generalization.

The paper ends here, and the authors set down how far their result holds. AssayBench-Loop gathers only genome-wide screens with sufficient signal, it is retrospective, and the policies evaluated on it await validation in a live experimental loop. The outcomes it handles are binary hit labels and nothing more. The budget is assumed equal in every round, and extending the framework to experiments that cost different amounts is left as future work. Noise between replicate experiments sits outside the model as well, so recorded labels are treated as fixed ground truth. That the test set holds 20 screens, and that those 20 were not drawn to represent all genome-wide screens, belongs on the same list, exactly as the appendix states.

Stepping one pace past what the paper says, the number 27.7% has a reverse side. Inside the same budget, the other 72.3% went unfound. That subtraction appears nowhere in the paper and belongs to this article. The authors present 27.7% as an achievement, and they are right to. On the same budget the established methods that leave past screens alone managed 14.5% at best and random selection managed 4.9%, so the comparison settles plainly enough.

In the room where someone decides whether to move this result into a lab, however, the question calls for amounts rather than ratios. Whether a target that mattered sat in the missing 72.3%, what finding it later would cost, and what one screen costs to run together decide whether assaying 5% counts as an achievement or as plain cost savings. The paper runs no such calculation. Its note that costs varying from round to round remain future work is the sentence closest to that ground.

One figure sitting quietly in the table enters the same calculation. Of the 1,000 genes AssayLoop picked, 7.6% fell outside the library of the screen in question. Part of the budget went out without being scored at all. The pool the policy draws candidates from is fixed at the 21,147 genes appearing in two or more screens, and the library any single screen actually measured is smaller than that. So the share that went outside mixes names that do not exist with real genes the screen never measured. The latter draws no penalty in the metric, while in a laboratory the reagents and the hours go out all the same.

One step further out of the paper, the material of this story is not CRISPR but records. Training ran on the decisions 1,349 screens left behind and the results those decisions produced, not on knowledge about genes. In most organizations such records do not survive. Outcomes get summarized into a line in a report, and what was tried in what order, and what was not, disappears in the act of summarizing. The result in section 4 ran precisely on the part that disappears.

So one question is worth taking from this paper back to your own organization. Does the list of what we attempted last quarter, together with the results, enter as input into deciding what to try first next quarter?

Thank you for reading this far. The paper is available at arXiv:2609.11877, and the figures in this article were checked directly against Table 1, sections 2.3 through 2.7, and Appendices A, B, H and K. If your team already has a way of feeding the history of experiments or operations back into the next decision, we would be glad to hear which items you keep.

• 1.Edwards, C., De Brouwer, E., Li, X., Lee, N., Hajiramezanali, E., Biton, A., Mostafavi, S., & Scalia, G. (2026). "Biology-in-the-loop: Amortized Adaptive Hit Discovery in CRISPR Screens." arXiv:2609.11877 (preprint, the primary source for all figures in this article).
• 2.De Brouwer, E., Edwards, C., Wu, A., Collier, J., Heimberg, G., Li, X., Subramaniam, M., Hajiramezanali, E., Richmond, D., Hütter, J.-C., Mostafavi, S., & Scalia, G. (2026). "AssayBench: An Assay-Level Virtual Cell Benchmark for LLMs and Agents." arXiv:2605.10876 (predecessor benchmark, cited in Section 2).
• 3.Genentech. "Genentech/AssayBench." GitHub (public benchmark code and data).