acceptodds
Under review as a conference paper at ICLR 2027

How Many Measured Genes Is a Prior Worth? Unseen-Perturbation Prediction as Decoding

Abstract

Models of transcriptional responses to genetic and chemical perturbations rarely beat the mean training response on unseen perturbations. We ask what a small measurement of the new perturbation would add, and whether its value can be predicted. Treating prediction as decoding, we note that without perturbation-specific information beyond the training set no architecture beats the mean response, predict the expected held-out error of linear measurements (a few genes or cells, or another cell line's response) from training perturbations alone with the classical risk of least squares, and bound combinations of training responses by a coverage floor. On five screens from three studies, the best tested zero-shot predictor recovers 7% to 30% of the recoverable signal and larger tested decoders at most 1.0 percentage point more, whereas four greedily chosen genes of the new perturbation (a simulated targeted readout) recover 33% to 75%; the best prior is worth about half of the first greedy gene on four screens (0.4 to 0.6 gene equivalents) and 3.4 genes on the fifth. With eight or more training perturbations per measured dimension, predictions track held-out errors (slope 0.97, , optimism 0.03) and choose panel sizes better than naive estimates, but are optimistic by about 0.11 below 100 training perturbations. Withholding a pathway raises the coverage floor from at most 13% to at least 33% of the held-out signal, and genes, priors and predictions fail; covering a quarter of it brings genes and predictions most of the way back.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
unseen perturbation prediction, virtual cell, single-cell perturbation screens, Perturb-seq, gene panel design, experimental design, predicting held-out error, zero-shot priors, distribution shift, rate-distortion

Reviews

Among:
Shape:
1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_wy6KOpenReview ↗
Rating
3
Confidence
1
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

This paper reframes unseen-perturbation response prediction as an information-decoding problem and asks whether prediction performance is primarily limited by model capacity or by the perturbation-specific information available to the predictor. Experiments across CRISPR and chemical perturbation screens show that increasing decoder capacity provides limited gains for the tested models, whereas a small number of measured genes from the new perturbation can substantially reduce prediction error. The paper further proposes a measurement metric for quantifying the value of prior information and shows that measurement performance can be predicted reasonably well from training data when the training set is sufficiently large.

Critical strengths
  1. Recasting unseen-perturbation prediction as a problem of available information rather than solely model capacity provides a useful perspective and connects prediction with experimental design.

  2. The proposed measurement equivalent offers an intuitive way to compare heterogeneous priors with direct experimental measurements. The finding that a few carefully selected genes can outperform the tested zero-shot priors is particularly relevant for experimental design.

  3. The paper develops theoretical results characterizing the zero-information limit, linear measurement channels, finite-sample prediction error, and a coverage floor for predictors that combine training responses.

Critical weaknesses
  1. The experiments consider several linear/kernel methods, MLPs, frozen pretrained representations, and a reduced-budget GEARS experiment, but do not evaluate fine-tuned foundation models or several competitive perturbation models. Therefore, the evidence more directly supports the claim that additional capacity provides limited gains among the tested models and representations, rather than a broader conclusion about model capacity in general.

  2. Gene panels are constructed from whole-transcriptome pseudobulk measurements rather than validated using an actual targeted measurement platform. Consequently, the reported advantage of a few measured genes may depend on measurement noise and assay characteristics that are not fully represented in the current experiments.

  3. The training-only prediction becomes noticeably optimistic with small training sets and can fail substantially under pathway-level distribution shifts. This limits its reliability precisely in settings where experimental guidance may be most valuable.

Questions for authors
  1. How would the main conclusions change with fully trained competitive perturbation models or fine-tuned foundation models? In particular, could stronger models extract more useful information from the same perturbation descriptors?

  2. How robust is the reported measurement advantage under realistic targeted-assay noise, dropout, and measurement constraints?

  3. Is it possible to construct a training-only diagnostic for coverage failure? Currently, the coverage floor becomes observable only after responses from the novel class have been measured, which limits its use for prospective experimental design.

  4. Given that the normalized error is energy-weighted and some chemical screens contain a small number of strong responders, would the main conclusions remain unchanged under an equally weighted per-perturbation metric?

2 comments
AuthorsOpenReview ↗

Three new analyses for Q2 to Q4 (simulated assay dropout and noise, a training-only coverage warning, an equal-weight metric); the capacity claim stated against the tested models and published fine-tuned benchmarks

We thank the reviewer for a precise review. Each question led to a change in the revised PDF (new text in blue): three new analyses (Tables 35 to 37; code in the supplement), explicit scope statements and, for readability, a setup sketch (Figure 1).

Q4: Equal weighting (new, Table 35). Each perturbation counts once: its error relative to that of the mean response, rpr_p, is averaged over perturbations.

Screenprior4 genesdifference [95% CI]weakest / strongest third
Norman singles0.990.70-0.29 [-0.35, -0.23]-0.32 / -0.24
Replogle0.930.88-0.04 [-0.05, -0.03]-0.13 / +0.02
A5491.020.89-0.13 [-0.18, -0.09]-0.22 / -0.07
K5620.990.84-0.14 [-0.18, -0.11]-0.16 / -0.12
MCF71.060.72-0.35 [-0.46, -0.26]-0.57 / -0.14

On this scale, which has no noise correction and so pulls every error toward 1, the margins are smaller but keep their sign, with intervals that exclude zero on every screen. The priors' gains sit mostly in strong responders: per perturbation no tested prior beats the mean response on A549 and MCF7, and on the chemical screens four genes gain most in the weakest third. The exception is the strongest third of Replogle, where Gene Ontology is level with or slightly ahead of four genes (+0.02 [0.00, 0.04]).

Q2: Assay noise and dropout (new, Table 36). We read the four genes from cells and corrupt every cell's readout, for training and held-out perturbations alike (dropout to zero expression; noise that multiplies the cell variance by 4), refit the decoder, and compare with the best prior on the same perturbations (paired bootstrap; (w) worse than the prior, (ns) not significant, unmarked better):

CellscorruptionNormanReplogleA549K562MCF7
best prior0.930.700.800.790.72
up to 128none0.600.67 (ns)0.470.420.23
up to 12850% dropout0.700.77 (w)0.520.490.27
up to 128noise x40.640.78 (w)0.530.530.26
up to 128both0.770.90 (w)0.73 (ns)0.72 (ns)0.34
10both0.96 (ns)0.99 (w)0.96 (w)0.99 (w)0.65 (ns)

Read from up to 128 cells, one corruption costs 0.04 to 0.11 and keeps the advantage on four screens; heavy corruption of a 10-cell readout erases it. The advantage thus depends on depth and readout quality, as you anticipated, and Replogle is the fragile case (it also loses from 5 cells, Table 18). This is a simulation on real cells, not a targeted platform, whose own biases and normalization we did not test (Limitations).

Q3: Training-only coverage diagnostic (new, Table 37). Before measuring, we compare the mean fingerprint similarity of a batch of new compounds to the training compounds with random batches drawn from training only. The alarm fires on 28 of 48 pathway hold-outs and 0 of 15 random folds, but the hold-outs it misses are still optimistic by 0.33 to 0.46. No rule that sees only descriptors can certify coverage in general: two classes with the same descriptors but different responses look alike before they are measured. A missing annotation (no training member of the pathway or target class) is the conservative trigger; here it is exact by construction. For such a class, the first members should be profiled in full; with a quarter of a pathway in training the forecast's optimism fell to 0.02 to 0.13 (Table 26).

Q1/W1: Stronger models. The submission already restricted the capacity claim to the tested families; the revision makes the gaps explicit (Section 5.1, Limitations). Tested: MLPs up to 7M parameters (at most 0.010 better, Table 30), frozen ESM-2, Geneformer and ChemBERTa (at most 0.7 genes, Table 28), the language-model-based GenePT prior (0.97 on the Norman singles, Table 29) and GEARS at a reduced budget. We did not fine-tune foundation models; published benchmarks, including fine-tuned scGPT and scFoundation, report the same pattern (Ahlmann-Eltze et al., 2025; Csendes et al., 2025). Whether a stronger model extracts more from the same descriptors is open, and Theorem 1 does not forbid it; the measurement equivalent prices any such model in genes on our folds.

W3: Small training sets and pathway shift. Section 6 now states the rule: optimism 0.01 with at least 200 training perturbations (only Replogle is that large), 0.07 with 100 to 199, 0.11 below 100 (Table 7). At smaller nn, the closed-form leave-one-out estimate, also training-only, has a bias of only -0.05 to +0.03 on every screen, including n=81n=81 (Table 9). Under pathway hold-out all three degrade: four genes rise to 0.68 to 0.93 (0.25 to 0.40 under random folds), still below the priors (1.02 to 1.04, Table 25), and the forecast turns optimistic by 0.35 to 0.57, which the warning flags in part.

We would welcome further questions.

I appreciate the authors' responses and the additional clarification they provided, I will keep my positive rating for your manuscript. By the way, I am interested in whether the used perturbations are common in this field, I would be sincerely grateful if you can answer (note that it is not necessary to respond).

Reviewer_9NEnOpenReview ↗
Rating
2
Confidence
1(−1)
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

The paper asks a question that seemed me to be quite interesting: If we want to predict how an unseen perturbation affects a living cell, how much information do existing statistical models (e.g., foundation models) provide? In order to quantify the gain, the expected information gain of a measurement of such a perturbation is used as a base-line unit (in my understanding, this is not yet revealing the answer as one would commonly perform many trials with such cell perturbations and gather averaged statistics).

The finding is that the information obtained by various statistical models is minimal for simple model and approaching the gain of a single actual measurement for sophisticated models. Whether the latter should be read as optimistic or pessimistic depends on the noise level of single measurements, which I am not familiar with and where I could not extract a clear answer from the paper in my attempts of reading it.

The experiments are accompanied with some information-theoretic considerations. Theorem 1 in the paper, to my understanding, provides a bit of an analog to the no-free-lunch principle: If the prior does not provide statistical information about the perturbation, its predictions are not very useful (one could just use a naive mean-predictor instead). For the further analysis, I had difficulties parsing the formalism, but it seems to formulate predicting impacts on gene expressions in perturbation experiments to basic linear channel-coding theory (Th. 2) and make some statements about overconfidence in training errors in linear (Gaussian) prediction models.

Overall, I find it very hard to assess the experimental, and even more so, the theoretical contribution of the paper. It seems to me that the overall question is intriguing, but I am not sure whether the insights are strong or obvious: In terms of theory, it seems obvious that limited information gives limited predictive power and that simple prediction models will be limited in gaining new information. In terms of experiments, the paper seems to confirm that biological systems can form complex emergent structures that are very hard to predict from observation of other, not directly related structures, i.e., we cannot make good predictions if we have not seem something very similar before in training. A single actual observation of a novel perturbation is thus highly informative. This sounds plausible but I am not able to assess whether this is a strong or obvious result.

To put my review into the right perspective, I should clearly state that I am not a biologist and have limited experience in bioinformatics, and I am not familiar with perturbation research. I am familiar with basic concepts of information theory and worked a lot on interdisciplinary applications of statistical learning, and I have some, although rather limited experience in applications to molecular biology. I would thus have expected to be able to understand a bit more of the ideas and findings. Whether the difficulty of gaining insights from reading the paper are due to my limited background or presentation issues of the current submission (that is my subjective impression at this point) should be left to reviewers more familiar with the subject area. In this sense, please treat the rest of the review with appropriate caution.

Critical strengths

At the current state of (in particular frontier-level) machine learning, the question of how far models are able to generalize in terms of highly complex patterns and structures in the natural world is a foundational problem. This is in particular a problem in natural and life sciences, such as understanding whole chemical landscapes from example MD simulations or predicting complex biological effects from other, not directly related observations. At the core, this asks about the complexity of emergent structures in our natural environment, and the amount of information inherent in them, and this will likely determine the fate of further scaling attempts (in the extreme, just to make the point: Whether we will see "runaway artificial super intelligence" or remain in strictly data-limited regime ultimately depends on whether still somewhat compact generic structure models exist or not, and the part of biology explored here is one where high complexity emergent structures have to be predicted, this is touches upon this question, generally speaking).

In this sense, the question posed by this paper (as I understand it) is highly relevant and very interesting: How much information does a statistical model of cell perturbations provide to a previously unseen scenario - this is exactly in line with the core issue of understanding whether some simple enough (reasonably low coding length) prior of biological patterns exists or not (here: at least at the level of models we have available right now). The answer of the paper seems to be rather pessimistic to me (I am not sure though), which is an interesting finding.

I also think that a framing of the problem in the general language of information theory can be helpful, as this, in the end, is the core issue (how much capacity does a "universal" prior for cell-biology need?).

My perception is that the paper is ambitious and addresses a foundational and important issue, and it proposes concrete ideas of how to quantify this (by considering split experiments and information gained through unseen single experiments).

Critical weaknesses

Unfortunately, my impression is that the paper needs at least some further work. Please note again, that the issues voiced below must be put into the perspective of a reader with limited background knowledge in this subfield of cell biology, which might be the causal factor for my still unfavorable perception.

  • The writing of the paper is very hard to follow. While the language is smooth and polished, decoding what the key problems, concepts and approaches are is surprisingly hard and I feel that I was only partially successful. One aspect is that very specific technical terms and jargon is brought up without a short positioning for readers with a more general background: On the life-science part, one has to read-up quite a bit of the problem background to understand what is going on. This is certainly not fully avoidable, but an abstract framing of the problem structure could still help a lot. In the part that deals with information theory, the discussion is dense, uses a lot of hard to decode notation (despite the - very extensive - Table 3 in the Appendix).

  • I am not convinced that the information theoretical analysis adds non-trivial insights. At least for Theorem 1, the assumption of no mutual information to the phenomenon to be predicted seems to put everything in a no-free-lunch scenario with obviously no hope for insights from training observations. I might be misunderstanding the statement, though.

  • The next two theorems would need a clearer discussion and positioning of why and how they are useful in the concrete problem setting. I was not able to decode this from reading the text multiple times.

  • On the experimental side, my understanding is that the unit of information gain everything is measured against is to provide a single sample of the delta in gene expression for a specific, previously unseen perturbation. If I understand this correctly (that might be a big if), the elephant in the room seems to be how much such a single measurement actually fluctuates. If the signal in terms of signal-to-noise-ratio was very weak, this could serve as an interesting measure. If not, it basically assesses how well generalization works when we do not have to generalize anymore. I would think that this deserves a broader conceptual discussion in the paper.

Overall I am skeptical in terms of the papers approach to presentation (which might very well be a personal bias) and I am a bit skeptical about the conceptual validity of the approach, both in theory and practice. At the latter part, I would at least expect a critical discussion of the fundamental issues of interpreting the results.

My personal assessment (now ignoring my personal uncertainties) would be that the paper in particular needs improvements in presentation/writing at the conceptual (what do discuss; language use is not an issue) level before one could fully assess its contribution and potential impact.

Questions for authors

Assuming that my rough understanding is not totally off: How strong is the main experimental finding - is it surprising that an actual measurement yields strong information compared to statistics of other perturbations? In terms of information theory derived: What is the main insight? Are there non-obvious / surprising consequences for this type of work?

In case my understanding is indeed lacking a lot, please say so. In that case I would alternatively appreciate a very short, general-audience-compatible summary of the main questions and insights (which would still benefit a revised version of the paper to be more accessible to the general audience of ICLR).

2 comments
AuthorsOpenReview ↗

A measured gene is one gene averaged over a median of 45 to 280 cells, scored on independent cells; what is non-obvious: priors priced in measured genes, forecast before measuring, with a measurable failure boundary

We thank the reviewer for a careful reading from outside the field and for incisive questions. Your reading is largely right (Theorem 2 is linear estimation, not coding); one refinement first: what lifts a prior is its side information, not its sophistication. Larger models gained at most 0.010 in error over kernel or linear ones (Table 30), and the best prior is worth 0.4 to 0.6 of one well-chosen measured gene on four screens, but 3.4 genes on Replogle (Table 2). The answer is thus pessimistic for priors and optimistic for small measurements, whose value can be forecast.

1. General-audience summary (now in the Introduction, with a sketch at the top of Figure 1). A perturbation (activating or silencing a gene, or adding a drug) changes gene expression; we predict this change, recorded on about 2,000 genes, for a perturbation absent from training. A prior predicts it without an experiment, from what is known (the gene's annotations, the drug's structure); a measurement reads a few of its entries on the new perturbation's own cells, and the rest is inferred from the training perturbations. Every prediction is scored on an independent half of the cells. We ask how many measured genes a prior is worth, whether this can be forecast before measuring, and where it fails. The main insight: the error is limited by the perturbation-specific information that reaches the predictor, so what a measurement buys can be computed before it is made.

2. What one measured gene is, and how noisy it is. It is not a single noisy sample of the response: it is one gene's change averaged over one half of the new perturbation's cells (a median of 45 to 280 cells per screen). Two facts address the "elephant in the room":

  • How noisy it is. New in Section 4: for the four chosen genes, the signal variance across perturbations is a median 5 to 7 times the noise variance of the readout (49 on the Norman singles), whereas 80% to 93% of all genes have more noise than signal on four screens. With fewer cells the advantage shrinks: from 5 cells, four genes lose to the prior on Replogle (0.88 vs 0.70, Table 18), and with simulated dropout plus noise on 10 cells it disappears (new Table 36).
  • It does not give the answer away. Measuring removes the need to generalize across perturbations, not across genes. The target is all of about 2,000 genes on the other half of the cells, and removing the four measured genes from it changes the error by 0.00 to 0.06 (Table 23): the gain is the prediction of unmeasured genes.

3. Is the finding surprising? What is non-obvious? That measuring helps is expected. What is not, and each could have failed:

  • The exchange rate above: on fixed folds and read depth, a currency in which any model can be priced.
  • It is known before measuring. With a few hundred training perturbations, Equation 2 forecasts held-out errors from training data alone (slope 0.97, R2=0.98R^2=0.98 at n/q≥8n/q\ge 8) and picks the best panel size on 4 of 6 screens, against 2 of 6 for naive estimates (Table 6).
  • Too few cells are worse than none. Theorem 2 predicts a cell count below which a raw measurement is worse than the training mean; the observed crossover brackets it on three screens and never occurs on the fourth, as predicted (Table 17).
  • A wrong message costs what the right one gains. Another perturbation's message raises the error 0.86 to 1.16 times as much as the correct one lowers it (Figure 2b; except the Norman singles), which argues against gains from variation shared across perturbations.
  • Your intuition, made measurable. That we cannot predict well what training has seen nothing similar to is, for predictors that combine training responses, Proposition 1: with a pathway absent from training, 33% to 47% of the held-out signal lies outside the span of the training responses (7% to 13% otherwise), and priors, measurements and forecasts fail together (Tables 25 to 27).

4. The theorems. We agree that Theorem 1 is a no-free-lunch statement and do not claim it as new. Its use is diagnostic: without perturbation-specific information no model helps, so a capacity sweep that stays flat at fixed inputs points to the inputs or to the training size, not to model size; on Replogle and K562 the priors still improve with training size yet trail four genes (Section 5.4). Theorem 2 turns a noisy measurement into an attainable error, with the two checks above; Theorem 3, the classical finite-sample risk of least squares, gives the forecast; Proposition 1 marks what no combination of training responses can reach. The tools are classical; the contribution is making each a prediction the screens could refute. A new passage says this in words (Section 3), and the new paragraph "Interpreting the results" (Section 6) discusses what a measured gene is and what is left to generalize.

New text is in blue. We would be glad to clarify anything that is still unclear.

Dear authors,

thanks for the answers and extensive discussion. From what I understand, when a perturbation is revealed, only half of the changes in gene expressions are observed, and the unobserved half is then predicted. Thus, the critical aspect is in how far these two halves are statistically dependent. I do not know enough of the relevant biology to assess that question, but it seems to me that it would be useful to discuss this aspect (even if this involves stating that exactly this has not been known at all prior to this paper). Nonetheless, if I understood this correctly, that would address one of the important potential issues I was concerned about in my review wrt. the experimental findings.

My recommendation at this point would be to still make a substantial further effort in improving the presentation of the paper (theory and experiments/biology) towards accessibility to a broader audience and emphasizing the key findings.

Update to the review: As a result of reading the other reviews and the authors' response, I have the impression that my knowledge of the specific area is insufficient to provide useful guidance towards the question of accepting the paper and I would advice the area chair towards putting most weight to the other reviews; I will lower my confidence score accordingly.

I would nonetheless stand by my assessment that presentation could still be improved substantially. This would include making it accessible to readers with slightly more adjacent background, but the general presentation could still be improved, such as giving a "bigger picture" assessment and discussion of the main theoretical and experimental findings and how relevant and how surprising they are. Whether this is a minor or major issue for the paper as a whole probably depends strongly on its impact on the application area studied, which I cannot assess.

Reviewer_RH1AOpenReview ↗
Rating
3
Confidence
1
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

In this paper, the authors study unseen perturbation prediction via an information theoretic lens, treating predictor as a message decoder. They 1) show that without perturbation-specific information no predictor beats the training mean, 2) predict the expected held-out error from training perturbations alone, and 3) show empirically that larger decoders do not improve on simple predictors, whereas a few measured genes do.

Critical strengths

The paper is well written and asks a practical question: what does a partial measurement buy, and can that be forecast before running it? The protocol is careful (batch-disjoint halves, training-only estimation, extensive sensitivity analyses). The authors are candid about failure regimes and pathway hold-out is a stress test of the “unseen” setting, which random folds do not really probe.

Critical weaknesses

I think the paper has limited actionability. The error forecast (Eq. 2) is optimistic throughout but it fails under pathway hold-out (Table 25), and the authors acknowledge this. And I don't see a proper quantification of when forecast could be trusted.

The capacity claim pertains to MLPs at most. While I understand the compute is a bottleneck, I think utilizing an API and querying larger foundational models could have made the paper stronger.

Questions for authors
  • In Figure 1.b, there seems to be overfitting with respect to genes measured, could the authors elaborate on it and why is this not happening for cell measurements?
  • Is it feasible for the authors to test a pre-trained model or an agentic/LLM-based predictor in a zero-shot setting, or elaborate on its cost alongside that of a targeted assay?
1 comment
AuthorsOpenReview ↗

When the forecast can be trusted, in numbers, plus a new training-only warning; why 32 genes overfit in Figure 1b while cells do not; frozen pretrained and GenePT priors priced in genes; fine-tuned models, LLM predictors and cost

We thank the reviewer for the positive assessment and the practical questions.

1. When can the forecast be trusted? (W1) Equation 2 forecasts an expected held-out error, and its accuracy depends on quantities known before measuring. The revision states them as a rule (Section 6, "Operating envelope"). Optimism is observed minus forecast ε\varepsilon, at n/q≥8n/q\ge 8:

ConditionOptimism of the forecastSource
fewer than 100 training perturbations0.11 on average (max 0.29)Table 7
100 to 1990.07 (max 0.23)Table 7
200 or more (only Replogle is that large)0.01 (max 0.05)Table 7
new pathway absent from training0.35 to 0.57 across linesTable 26, c=0c=0
a quarter of that pathway in training0.02 to 0.13 across linesTable 26

So the forecast is accurate to a few hundredths on average with at least 200 training perturbations, eight per measured dimension, and training members of the new perturbation's class; it should not be used for an unrepresented class, whose first members should be profiled in full. At smaller nn, the closed-form leave-one-out estimate, also training-only, has a bias of only -0.05 to +0.03 on every screen, including n=81n=81 (Table 9); Equation 2 adds the explicit dependence on nn and qq.

Actionability. The forecast's job is to choose how much to measure: Equation 2 picks the best panel size on 4 of 6 screens (mean regret 0.036), against 2 of 6 (0.121) for naive training-error estimates (Table 6).

New: a training-only warning (Table 37). For a batch of new compounds, the mean fingerprint similarity to the training compounds is compared with random batches drawn from training only. The alarm fires on 28 of 48 pathway hold-outs and on none of 15 random folds, but the hold-outs it misses are still optimistic by 0.33 to 0.46. Similarity is a warning, not a certificate; the conservative trigger is an annotation: no training member of the new perturbation's pathway or target class (Section 5.4).

2. Figure 1b versus 1c (Q1). Equation 2 reads ED=Lq(1+1n)n−2n−q−2,\mathbb{E}D = L_q\Big(1+\frac{1}{n}\Big)\frac{n-2}{n-q-2}, where LqL_q is the best error attainable with a qq-dimensional message and the factor after it is the cost of fitting q+1q+1 coefficients per gene from nn training perturbations. For a gene panel, q=kq=k. With n=81n=81 (Norman singles) that factor grows from 1.27 at 16 genes to 1.70 at 32, with n=145n=145 (sci-Plex K562) from 1.13 to 1.30, and the least-squares decoder overfits. This happens on the four screens with at most 145 training perturbations, at n/q=2.5n/q=2.5 to 4.5, outside the regime n/q≥8n/q\ge 8 in which the figure draws the forecast; there Equation 2 predicts the rise on the three sci-Plex lines but underestimates it, and misses it on the Norman singles. With 181 or more training perturbations the error keeps falling (on Replogle, n=1,294n=1{,}294, the factor stays between 1.01 and 1.03). For cells, the message is projected on q=8q=8 training directions whatever the number of cells, so more cells lower its noise without adding coefficients. This explanation is now in Section 5.2.

3. Pretrained models, LLM-based predictors and cost (W2, Q2). Pretrained models were tested zero-shot: frozen ESM-2, Geneformer and ChemBERTa embeddings are worth at most 0.7 measured genes (Table 28), and a prior built from a language model, GenePT embeddings of each gene's text description, reaches ε=0.97\varepsilon=0.97 on the Norman singles (Table 29). The submission already restricted the capacity claim to the tested families; the revision states the remaining gaps explicitly (Section 5.1, Limitations) and cites published benchmarks with fine-tuned models that report the same pattern: five foundation models and two other deep models did not outperform simple baselines (Ahlmann-Eltze et al., 2025), and the mean of the training perturbations outperformed fine-tuned scGPT and scFoundation (Csendes et al., 2025). We did not query an LLM or an agent. Such a test is feasible, but a success would be hard to read: our screens (2019 to 2022) are likely in a model's training data, so only a failure would be clear-cut, and a clean test needs screens released after the model's cutoff. An agent that retrieves literature would add side information, which Theorem 1 allows to help; the measurement equivalent would then price it in genes on the same folds.

Cost. A prior needs no experiment, and our whole pipeline, all priors included, runs in about 20 hours on a laptop (GEARS: about 45 minutes per fold). A measurement still requires running the perturbation; a targeted readout reduces sequencing (TAP-seq reports up to 50-fold lower requirements), but we did not measure costs and claim no saving. What the paper adds is the other side of the trade: how much each measured gene buys, known before paying for it.

New text is in blue in the revised PDF. We are glad to answer follow-up questions.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

Related papers

Loading the map…

Discussion (0)

Sign in to comment.