acceptodds
Under review as a conference paper at ICLR 2027

CREST: Contrastive Metric Learning for Perturbation Modeling and Retrieval

Abstract

In target and drug discovery, the vast combinatorial space of genetic and chemical perturbations makes exhaustive screening intractable, positioning candidate retrieval – the in silico prioritization of promising conditions for physical validation – as a central practical application. Yet current models frequently fail to generalize across unseen cellular contexts, suffering from mode collapse, a behaviour which is encouraged by pointwise reconstruction losses that lack geometric constraints to separate distinct perturbation signatures. To address this, we present CREST (Contrastive Retrieval of Expression State Transitions), a metric learning framework that co-embeds context-conditioned perturbation queries and measured transcriptional responses in a shared space via contrastive alignment. On LINCS L1000 profiles, CREST substantially outperforms all evaluated baselines on candidate retrieval under cell line holdout, and as context diversity scales up to 86 training cell lines, CREST exhibits near-linear gains in retrieval, while capacity-matched pointwise models remain nearly flat. CREST’s discriminative space flexibly extends to transcriptional response prediction: retrieving nearest-neighbor reference profiles for unseen queries yields response estimates that outperform dedicated models. Moreover, simply swapping the reference profiles at inference enables the frozen, bulk-trained CREST to transfer zero-shot to single-cell Perturb-seq, outperforming specialized single-cell models across unseen conditions. Overall, CREST establishes contrastive metric learning as a scalable foundation that unifies candidate prioritization and perturbation response prediction within a single geometric framework.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
contrastive learning, context-conditioning, metric learning, perturbation retrieval, perturbation prediction

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_mKBYOpenReview ↗
Rating
3(+2)
Confidence
4
Informativeness
2(+1)
Presentation
3
Soundness
2
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Paper summary

The authors of CREST propose a metric learning framework that learns a shared representation of perturbation-context effects on cells and uses it for retrieval on previously unseen cell lines or to predict perturbations' effects. CREST outperforms simple baselines on the LINCS1000 dataset, and it also shows promising results on the Replogle RPE-1 dataset in a cross-assay experiment.

Critical strengths

The paper is mostly well written, and the abstract and introduction are engaging. The authors clearly define the general problem and provide a convincing rationale for their approach. I like Figure 1, and I think it is a good summary of the work. I would slightly increase the font size and change the orange font to another colour, though - currently it's barely legible. I appreciated appendices E and F, though some of that material should definitely move to the main text to support important claims.

Critical weaknesses

I am not entirely convinced of the novelty of the approach and of its effective contribution to the field. The methodology is indeed not new, as contrastive alignment with all the subsequent machinery and softmax-kNN retrieval/prediction are well documented and established in different domains and applications. As far as the specific application is concerned, I believe there is some adjacent work that predates this study.
Conceding that what is stated above is debatable, I have some other concerns:

  • The results are measured only on 1 dataset per type of experiment, on 3 different seeds rather than splits, and no statistical test has been performed. Moreover, the splits for the main results have very limited val and test sizes;
  • I believe the empirical attribution is not sufficiently solid: the comparison does not isolate contrastive learning from retrieval-based prediction, dimensionality of latents, or trivial averaging effects. Some elements in the architecture have not been ablated, such as the k elements in the top-k retrieval, or competing baselines' parameters;
  • This approach is trivially bound to fail whenever any queried perturbation-context tuple falls outside the convex hull of the measured reference responses. As I understand it, this model has no way to avoid this, and no uncertainty measure could ameliorate it.

Overall, I think this paper is not ready for publication as is, but I am willing to reconsider if persuaded.

Questions for authors
  • Q1: Can the authors compare CREST against simpler retrieval-based baselines, such as PCA-kNN and MSE+kNN, and evaluate CREST with an unconstrained regression decoder? This would help disentangle the contributions of contrastive learning, retrieval, and averaging.
  • Q2: Can the authors extend the evaluation to additional datasets or, alternatively, explore different train/test splits to assess robustness and out-of-distribution generalization? In particular, I would appreciate confidence intervals across independently held-out cellular contexts, as well as experiments involving unseen compounds or scaffold-based splits.
  • Q3: Can the authors disentangle the effects of context diversity and training-set size? For example, could they compare models trained on the same number of observations drawn from different numbers of cellular contexts?
4 comments

We thank the reviewer for the careful reading, the concrete experimental suggestions, and the openness to reconsideration. We have tried to address each point directly in the revised manuscript.

Novelty. We agree that contrastive alignment and softmax-kkNN are established building blocks; our intended contribution is how they are formulated and combined for candidate prioritization and perturbation modeling (G1). As detailed in Section 3 (see also G3 and Reviewer 1, Item 1), conditioning perturbation embeddings on measured CCLE expression via gated cross-attention before contrastive alignment, rather than operating on unconditioned representations or text descriptions, yields large gains over our PertOmni-style encoder across Condition Retrieval@10, Context Retrieval@1 (Table 1), and cross-modality gene KO–compound matching (Table 2c).

Evaluation and statistics. Please see G2. All LINCS experiments now use five cell line holdout splits rather than one split with three seeds, reported as mean ±\pm SD across splits (Section 4.1, Tables 1–3) and per held-out cell line across the three splits (Appendices G, L, and M).

Contrastive objective and hyperparameter ablations.

  • Retrieval and averaging: Matched MSE/wMSE backbones paired with softmax-kkNN (Appendix N) and PCA-kkNN (Tables 1, 3) use the identical retrieval and averaging readout yet remain well below CREST (G3).
  • Latent dimensionality: CREST, the matched backbones, and the PertOmni-style encoder were retrained across d∈{64,128,256}d \in \{64, 128, 256\}; CREST leads at every dimension (Appendix E).
  • kk and TT: We now select both on each split's validation cell line from k∈{1,5,10,20,50,100}k \in \{1, 5, 10, 20, 50, 100\} and T∈{0.03,0.1,0.3,uniform}T \in \{0.03, 0.1, 0.3, \text{uniform}\} for every retrieval-based model and modality (Appendix A), allowing the readout to adapt to reference atlas size and modality density.
  • Baselines' parameters: Appendix E sweeps each baseline's main hyperparameter (ridge α\alpha, random forest and XGBoost depth, TabICL estimators, and embedding dimension dd); none approaches CREST.

Reference atlas coverage and convex-hull limitations. Please see G4. We agree that non-parametric retrieval cannot extrapolate beyond the convex hull of reference responses, and Section 5 now states this limitation explicitly. Within that same convex hull, however, the Table 3 oracle and fixed-atlas scaling analysis (Figure 3, Appendix P) show that better representations and neighbor weighting steadily improve predictions from the exact same reference set, indicating substantial headroom within existing atlas boundaries.

Presentation. The response-projector pathway enrichment and cross-cell-line MoA-coherence analyses have been moved into the main text (Section 4.3, Figure 2, Table 2a,b). For Figure 1, we have increased the label font sizes and replaced the low-contrast orange text with a higher-contrast color.

Q1. Please see G3 and Contrastive objective and hyperparameter ablations above for the PCA-kkNN and matched MSE/wMSE+kkNN retrieval controls (Appendix N). For the unconstrained regression-decoder comparison, the matched MSE and wMSE backbones (Table 3) pair the identical condition encoder with a linear decoder trained via reconstruction loss rather than contrastive retrieval.

Q2. Please see G2 for our five cell line holdout splits, per-line mean ±\pm SD across held-out contexts (Appendix L), strict chemical out-of-distribution evaluation on structurally novel compounds (Tanimoto similarity ≤0.4\le 0.4; Appendix F), and context-similarity analyses (Appendices G and M).

Q3. We agree that adding cell lines in the scaling analysis (Section 4.5) also increases total training data, confounding the two effects. We therefore added a controlled ablation (Appendix Q) that varies context diversity while holding training-set size fixed. Specifically, gene-KO CREST models are trained on the same 4,0004{,}000 knockouts, each observed in rr cell lines (N=4,000rN = 4{,}000r total profiles) distributed across L≥rL \ge r training cell lines, with the held-out test set kept identical across all configurations. Comparing settings with the same NN but different LL isolates context diversity: spreading a fixed number of observations across more cell lines consistently improves Condition Retrieval@10, whereas increasing the number of observations per knockout (rr) yields a substantially larger gain. Thus, context diversity improves generalization beyond data volume alone, though data volume remains the dominant driver at this scale.

First, I really appreciate the care and effort put into the rebuttal. The authors have clearly tried their best to accommodate my requests and concerns.

  • Figure 1 is much more readable now - well done.
  • Evaluation and statistics have been partially addressed; I would still like to see the statistical tests. The evaluation is overall a bit limited by the fact that the splits involve only five distinct held-out cell lines, and the primary experiments still rely on a single dataset. The new chemical OOD experiment is appreciated, although the results look relatively modest. CREST's Retrieval@10 performance on structurally novel compounds is very close to PCA-kNN and Latent Additive. I believe this deserves more emphasis when discussing generalisation to previously unseen perturbations.

As a general recommendation, I believe empirical ML studies should always quantify the uncertainty associated with reported performance estimates and support comparative claims with appropriate statistical tests. Reporting point estimates alone is rarely sufficient to establish that observed improvements are robust or statistically meaningful. I would encourage the authors to follow this advice in the future, following established practices in statistical learning and model evaluation.

  • Discrepancy of results: there is a difference between the original and revised discrimination-rank results. In the revised Table 3, the per-perturbation mean baseline slightly outperforms CREST on discrimination rank in both modalities, while PCA-kNN is also very competitive. Could the authors clarify if these differences are attributable to the revised splits, or whether the evaluation protocol, metric implementation, or retrieval configuration has also changed?
  • Convex-hull limit. I appreciate the additional analyses and the explicit acknowledgement of the convex-hull limitation. The fixed-atlas scaling experiment is particularly useful in separating representation quality from reference coverage. Still, the oracle comparison does not resolve the extrapolation limitation, since the oracle selects reference responses using information from the ground-truth test response. I still think introducing a measure of uncertainty or OOD-reliability would be valuable for practical applications, although I recognise that addressing extrapolation directly may be beyond the scope of the proposed retrieval framework.
  • learned geometry. Moving the pathway enrichment and MoA-coherence analyses into the main text is a welcome improvement, as is the new gene KO–compound retrieval experiment. I still find the biological interpretation somewhat stronger than the supporting evidence. The MoA-coherence analysis measures similarity within biological mechanisms, but does not establish how effectively distinct mechanisms are separated. I think this would require a set of experiments that perhaps would not fit too well into this narrative, so I would suggest reconsidering the narrative instead.

OVERALL

The rebuttal has substantially improved my assessment of the paper. In particular, the additional retrieval baselines, hyperparameter analyses, multiple holdout splits, and controlled scaling experiments address several of my original concerns convincingly. My remaining reservations concern primarily the degree of methodological novelty, the limited diversity of biological evaluation settings, and the strength of the claims regarding the learned representation's biological meaning and generalisation capabilities.

I recognise the value of the proposed framework and the empirical improvements demonstrated by the authors. I suggest that the other reviewers consider these elements before the final discussion, too.

I believe these remaining limitations prevent me from supporting acceptance at this stage. In recognition of the substantial improvements and the authors' constructive response, I am raising my recommendation from clear rejection to weak rejection.

We thank the reviewer again for carefully re-evaluating our revised manuscript, for recognizing the substantial improvements made during the rebuttal, and for raising your assessment of our work. We briefly address each of your remaining points below:

  • Figure 1 readability. Thank you!

  • Evaluation, statistical tests, and chemical OOD generalization.

    • Statistical tests & uncertainty: We have now added paired statistical tests alongside split-level standard deviations across the manuscript to better ground comparative claims.
    • Chemical OOD generalization: In Section 4.2 and Table S5, we now explicitly emphasize that while CREST matches or outperforms baselines on structurally novel compounds, absolute retrieval accuracy remains modest across all methods. We also note in Section 5 that incorporating richer molecular and biological priors and/or featurizations is an important next step for out-of-vocabulary and OOD perturbations.
  • Discrepancy in discrimination-rank results. Thank you for catching this difference, and we apologize for forgetting to note it earlier. The change stems from how CREST's predictions were scored rather than from the splits or metric implementation: in the initial submission, CREST's discrimination rank was computed using cosine similarities in CREST's learned embedding space (via WW). However, given that the task in Table 3 is transcriptional response prediction—and to ensure a fair, apples-to-apples comparison across methods—we decided it was more appropriate to evaluate CREST using its softmax-kNN-predicted profiles directly in expression space, matching how all other response prediction baselines are scored (Table 3, Appendix C).

  • Convex-hull limitation and OOD reliability. We agree that the empirical oracle does not resolve the convex-hull extrapolation limit, as it selects from the same reference atlas using ground-truth target shifts. Our cell-line holdout and multi-context single-cell evaluations partially probe cross-context generalization (Sections 4.2, 4.4, and 4.6), and our cross-line similarity analyses (Appendices G and M) show that baseline transcriptional similarity to the nearest training line strongly correlates with CREST's retrieval and response prediction accuracy. While this similarity can provide a practical indicator of OOD reliability, we agree that more directly assessing OOD responses for transcriptional response prediction would be valuable directions for future work.

  • Learned geometry and biological interpretation. Thank you for the feedback on moving the pathway enrichment, MoA-coherence, and gene KO–compound matching analyses into the main text. Following your suggestion, we revised Section 4.3 to better align our framing with the supporting evidence, focusing on CREST's preservation of shared mechanistic similarity across cellular contexts rather than claiming separation between distinct biological mechanisms.

Finally, as mentioned in our latest general comment above, we have added a new evaluation on a multi-context single-cell Perturb-seq inverse retrieval benchmark (Section 4.6, Appendix R). We hope that this new single-cell benchmark, together with the added statistical tests and calibrated biological narrative, addresses your remaining concerns, particularly regarding the diversity of biological evaluation settings.

Thank you for working on this and updating the manuscript. I am much happier with this current version; it is now a much stronger and more appropriate comparison and study. I am still relatively unsure of the fairness of some of the comparisons, but I acknowledge that this is a tough task (first-hand experience), and I am willing to reward the excellent responsiveness and work done in the last couple of weeks. I am sorry my colleagues did not interact as much with your work, but I hope my comments helped improve this work. Please finish adjusting the narrative and tidying up the text. I thank you for your work and raise my score to weak accept (cannot, in all fairness, ignore my last doubts). Best, mKBY

Reviewer_J6zbOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper proposes CREST, a contrastive metric learning framework for perturbation response retrieval and prediction. The method jointly embeds perturbation–cell context pairs and measured transcriptional responses into a shared representation space using a contrastive objective. Instead of directly predicting expression profiles through a regression decoder, CREST retrieves similar responses from a reference atlas and combines them to generate predictions. The authors evaluate the framework on LINCS L1000 under cell-line holdout, investigate performance scaling with increasing numbers of training cell lines, and demonstrate cross-assay transfer to a single-cell Perturb-seq dataset. CREST reports substantial improvements over the evaluated baselines, particularly on retrieval and perturbation discrimination metrics.

Critical strengths

S1. The paper aims to tackle an important problem in perturbation modeling, particularly the difficulty of predicting perturbation-specific transcriptional responses across unseen cellular contexts. Reformulating perturbation response prediction as contrastive metric learning followed by reference-based retrieval is an interesting alternative to conventional regression approaches. The framework also provides a unified way to perform candidate retrieval and transcriptional response prediction.

S2. The reported improvements are substantial on the evaluated LINCS L1000 benchmark. In particular, CREST improves both retrieval accuracy and perturbation discrimination compared with the matched regression models and simple mean baselines. The scaling experiments are also useful, showing a clear improvement in performance as the number of training cell lines increases. The inclusion of both genetic and chemical perturbations, as well as the attempt to evaluate transfer to single-cell data, is also valuable.

Critical weaknesses

W1. My main concern is the limited diversity of datasets and evaluation settings. Most experiments are conducted on a single LINCS L1000 dataset, with only three held-out cell lines used to evaluate generalization. Although the training dataset contains many cell lines and perturbations, evaluating on only three cell lines makes it difficult to determine whether the reported improvements generalize across different biological contexts. The external validation is also limited to one RPE-1 Perturb-seq dataset. Moreover, the main cross-assay comparison in Table 3 is based on only 37 test perturbations shared across the evaluated methods. In the expanded evaluation in Appendix J, the linear prediction model substantially outperforms CREST on the discrimination rank metric. These limitations make the broad claims about generalizable perturbation modeling and cross-assay transfer less convincing.

W2. The baseline comparisons are not sufficiently comprehensive, and the comparison between contrastive learning and regression does not fully isolate the contribution of the training objective. The LINCS experiments primarily compare CREST against classical regression methods, TabICL, and matched MSE or weighted MSE models, without including representative recent perturbation prediction approaches discussed in the Related Work section. More importantly, the matched regression models predict expression profiles through a 128-dimensional linear decoder, whereas CREST retrieves and combines full-dimensional measured expression profiles from a reference atlas. Therefore, the performance difference may reflect both the contrastive training objective and the different prediction mechanisms. A more informative comparison would apply the same reference-based retrieval procedure to an MSE-trained encoder, allowing the contribution of contrastive learning to be evaluated more directly.

W3. A fundamental limitation of CREST is its dependence on the coverage of the reference atlas. Since predictions are constructed as weighted combinations of measured reference responses, the model cannot generate transcriptional response patterns outside the convex hull of the available signatures. This limitation also complicates the interpretation of the scaling results in Figure 3. As the number of training cell lines increases, the reference atlas may provide more representative neighbors for test queries, so the observed improvement could reflect better reference coverage rather than more transferable representations. The authors should disentangle these two factors by evaluating encoders trained at different scales against a fixed reference atlas. It would also be informative to examine how much the retrieved neighbor sets overlap across different queries and how often the same perturbation is retrieved from other cellular contexts. Finally, the zero-shot cross-platform evaluation relies on measured responses from the target Perturb-seq dataset, rather than predicting single-cell responses independently of target platform. These dependencies should be made clearer when discussing the generalization and scaling capabilities of CREST.

Questions for authors

Q1. How much of the observed improvement comes from contrastive learning rather than the reference-based prediction mechanism? Can the authors evaluate an MSE-trained encoder using the same retrieval and aggregation procedure to better isolate the contribution of the training objective?

Q2. In the scaling experiments in Figure 3, is the reference atlas kept fixed across different training fractions, or does it grow with the number of training cell lines? If the atlas also grows, the improvements in perturbation prediction may partly reflect better reference coverage rather than improved representation learning. Can the authors disentangle these two factors, for example by evaluating encoders trained at different scales using the same fixed reference atlas?

Q3. How sensitive is CREST to the coverage of the reference atlas, particularly in the cross-platform experiments? Since the zero-shot transfer to Perturb-seq still relies on measured responses from the target dataset, can the authors evaluate how performance changes when the target reference atlas is reduced or when responses from the same perturbation are excluded?

1 comment

We thank the reviewer for the detailed and constructive review, and for the suggestions on isolating the training objective and examining the role of the reference atlas.

W1. Evaluation diversity. Please see G2 for our expanded five-split LINCS evaluation across five held-out cell lines and added out-of-distribution analyses (Appendices F, G, L, and M). For the cross-assay experiment (Section 4.6), Table 4 restricts the main comparison to the 3737 test perturbations covered by all published models so that every method is scored on identical queries, whereas Appendix R reports results on a broader perturbation panel. As Section 4.6 notes explicitly, we agree that the linear model achieves a stronger discrimination rank on that broader panel because it is trained directly in-domain on RPE-1, while CREST is applied zero-shot without fine-tuning (and still leads on Pearson Δ\Delta). In line with our reframed Abstract and Section 1 (G1), we frame this experiment as evidence of cross-assay transfer of the learned condition space rather than as a comprehensive single-cell benchmark. Expanding the Section 4.6 single-cell benchmark is currently a work in progress, and we will provide updates shortly.

W2 and Q1. Objective versus prediction mechanism. We followed the reviewer's suggestion to include this control (G3, Appendix N). When matched MSE and wMSE backbones—retrieving with either decoded profiles or latent embeddings—and unlearned PCA-kkNN features are paired with CREST's exact softmax-kkNN readout over the same reference atlas, all remain substantially below CREST on both Pearson Δ\Delta and discrimination rank (Table 3, Table S8). These controls confirm that the gains stem from the contrastively learned representation geometry rather than the retrieval readout.

W3 and Q2. Atlas coverage and scaling. Please see G4. Unlike the original Figure 3, where the reference atlas grew with the training set, all models in the revised scaling analysis retrieve from the same full reference atlas at every training fraction (Section 4.5, Figure 3, Appendix P), confirming that scaling gains reflect improved representation quality rather than atlas growth. Appendix O further details the retrieved atlas neighbors (G4), showing that CREST consistently retrieves the queried perturbation across cell lines while keeping top-5050 neighbor sets perturbation-specific rather than confounded by cell line identity.

W3 and Q3. Dependence on the target platform. Please see the above response to W3/Q2 regarding CREST's sensitivity to reference atlas coverage. With respect to the cross-platform Perturb-seq evaluation (Section 4.6), we agree that zero-shot transfer relies on measured responses from the target platform (while the condition encoder transfers zero-shot), and Section 5 now states this dependence and its convex-hull bounds more explicitly (G4). We also note that in our current RPE-1 benchmark (Section 4.6), splits are partitioned by perturbation, so responses from the queried test perturbation are already excluded from the target reference atlas. Our additional experiments and revisions for Section 4.6 are still a work in progress, and we plan to share those updates shortly.

Reviewer_aYT2OpenReview ↗
Rating
2
Confidence
4
Informativeness
1
Presentation
3
Soundness
3
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Paper summary

The authors introduce CREST, a method for perturbation response modeling. The main observation is that existing methods often use mean squared error (MSE) objectives, which can encourage models to predict mean-like responses and reduce their ability to discriminate between different perturbation effects. To address this, the authors introduce a contrastive loss based on InfoNCE, which brings representations of matching perturbation–cell-context queries and measured transcriptional responses closer together while pushing mismatched representations farther apart. They then use this learned representation space for retrieval: given a perturbation and cellular context, the model identifies the closest measured response profiles and combines them to predict the transcriptional response. The authors demonstrate improved performance compared with the evaluated baselines on retrieval and perturbation response prediction, including transfer to a single-cell perturbation benchmark.

Critical strengths

As someone who works with virtual-cell models and has trained some of these models, I agree that using mean squared error and related pointwise losses can lead to a collapse in discriminability, where models tend to predict mean-like responses because doing so minimizes the loss. This is definitely an important problem in the community. I also think the attention mechanism is interesting. Conditioning the perturbation representation on a contextual vector derived from the baseline expression of the cell line is an interesting approach. While the broader idea has already been explored, this particular conditioning mechanism may offer some novelty.

Critical weaknesses

First, I think the biggest problem is the selection of baselines. The paper acknowledges that existing methods have already explored similar ideas, including approaches such as PertOmni and earlier work on aligning perturbation and transcriptional response representations. However, these methods are not included in the benchmarks. There needs to be an actual comparison against methods that do essentially the same thing: use contrastive objectives in a latent space to improve perturbation representation learning and retrieval. Without these comparisons, it is difficult to assess the novelty and significance of the reported improvements. Related to novelty, there is no ablation of the context-conditioning mechanism, given how methods exist already doing contrastive learning in this space, this ablation could help demonstrate the novelty of this work relative to existing work.

Second, in the single-cell perturbation-effect benchmark, there are other, more recent models that could be considered beyond those included in the paper. These include models such as STATE, which is cited in the paper but not evaluated. The authors should consider including more recent baselines or explain why these methods were excluded.

Lastly, I think the evaluation is somewhat limited in terms of the datasets used. The primary experiments are conducted on LINCS L1000, with only three held-out cell lines, and the single-cell experiments are limited to one additional dataset. There are now several readily available perturbation benchmarks, such as PerturBench, that provide diverse datasets and standardized evaluation settings. Given that a central claim of this work is improved generalization across cellular contexts and perturbation responses, it would be valuable to evaluate the method across a broader range of datasets to demonstrate that these improvements are robust and not specific to the LINCS L1000 setting.

Questions for authors

See weaknesses

1 comment

We thank the reviewer for the thoughtful review and for recognizing both the prevalence of mode collapse under pointwise losses and the potential of our context-conditioning mechanism. We also appreciate the feedback on positioning; as noted in G1, we have reframed the Abstract and Section 1 around candidate prioritization and elevated our biological grounding and cross-modality retrieval analyses into Section 4.3.

1. Contrastive baselines and ablation of the context-conditioning mechanism. Please see G3. To the best of our knowledge, prior contrastive frameworks in this area have not directly paired context-conditioned encoders over measured expression profiles with contrastive alignment for perturbation retrieval: existing contrastive methods generally align unconditioned representations with imaging readouts (e.g., CLOOME, MolPhenix, CellCLIP), making PertOmni (which uses text-derived context descriptions rather than measured expression) the closest counterpart. Because no public implementation of PertOmni is available, our PertOmni-style encoder (Appendix C) holds CREST's response projector, contrastive objective, and retrieval fixed while replacing gated cross-attention over measured CCLE expression with PertOmni's text-derived embeddings. This directly isolates our conditioning design, where CREST leads across all retrieval metrics (Table 1), embedding dimensions (Appendix E), and training-set sizes (Figure 3).

2. Recent single-cell baselines. We first aimed to address this on our primary LINCS L1000 benchmark by adding PerturBench's Latent Additive model alongside the PertOmni-style contrastive encoder (see G3). For the zero-shot single-cell transfer experiment (Section 4.6), our current Table 4 and Appendix R compare against the published model outputs curated and re-scored by Ahlmann-Eltze et al. to ensure a direct comparison on identical splits without re-tuning third-party models. Expanding the Section 4.6 single-cell benchmark is currently a work in progress, and we will provide updates shortly.

3. Dataset breadth. Please see G2 for our expanded five-split LINCS evaluation (9191 cell lines) and out-of-distribution analyses (Appendices F, G, L, and M). We focused on LINCS L1000 because single-cell benchmarks in suites like PerturBench typically span only a few cell types and a single modality, whereas evaluating cross-context scaling and cross-modality retrieval requires broad multi-line, dual-modality coverage. Training directly on emerging multi-context single-cell atlases (Sections 1 and 5) is a natural next step.

Comments on the paper

4 comments
AuthorsOpenReview ↗

Summary of Revisions

We sincerely thank the reviewers for their careful, fair, and helpful reviews. We hope that our efforts to address the main gaps identified by the reviewers have made the paper substantially stronger. Below, we first summarize the revisions shared across reviewers (G1–G4) and then respond to each reviewer individually. All cited sections, tables, and figures refer to the revised manuscript. Changes addressing the reviewers' comments are highlighted in orange.

G1. Clarifying our focus on candidate prioritization and biological grounding. The reviewers' comments helped us recognize that our original manuscript could have more clearly articulated the framing and direction of our work. Rather than aiming to be another virtual cell model focused primarily on transcriptional response prediction, CREST centers on candidate prioritization—ranking perturbation–context pairs for experimental validation, while supporting response prediction via retrieval. We made light revisions to the Abstract and Introduction to clarify this goal. To reinforce this focus, we elevated the response-projector pathway enrichment and cross-cell-line MoA-coherence analyses into Section 4.3 (as suggested by Reviewer mKBY) and added a cross-modality prioritization task: given a held-out gene KO response, CREST retrieves on-target compounds among 1,0001,000 candidates (Table 2c, Appendix J), with CREST outperforming all baselines.

G2. Broader evaluation, dataset diversity, and out-of-distribution analyses. We evaluate on LINCS L1000 because it is the largest harmonized resource spanning both genetic and chemical perturbations across many cellular contexts (130,554130,554 pairs across 5,1405,140 CRISPR KOs, 9,6659,665 compounds, and 9191 cell lines; Section 4.1), providing the context breadth required for multi-line holdout. All LINCS results now use five cell line holdout splits instead of one split with three seeds (Tables 1–3) and per held-out cell line (Appendix L). The held-out cell lines were selected as those profiling at least 4,0004,000 gene KOs and 1,0001,000 compounds (Section 4.1), ensuring dense dual-modality coverage across distinct lineages. We also added two out-of-distribution analyses:

  • Structurally novel compounds (Section 4.2, Appendix F): On unseen test compounds with maximum Tanimoto similarity ≤0.4\le 0.4 to any training compound, CREST matches or outperforms all competing baselines, though generalization on this strict chemical OOD split remains modest across all methods.
  • Cellular context proximity (Appendix G and M): Baseline expression similarity to the nearest training line correlates strongly with both Condition Retrieval@10 (Section 4.2) and Pearson Δ\Delta correlation (Section 4.4).

G3. Stronger baselines and readout-isolation controls. We added three baselines to every main table (Tables 1, 2c, and 3): (i) a PertOmni-style contrastive encoder—built using CREST's response projector, contrastive loss, and retrieval paired with PertOmni's text-based cell line and GO/GenePT featurization (Appendix C); (ii) PCA-kkNN, a training-free baseline applying CREST's softmax-kkNN readout to the regressors' input features (Appendix C); and (iii) PerturBench's Latent Additive model (Appendix C). CREST leads across all main metrics (Table 1), alongside the highest Pearson Δ\Delta correlation in both modalities (Table 3). Moreover, combining alternative representations (the PertOmni-style encoder, PCA-kkNN, and matched MSE/wMSE backbones) with the exact same softmax-kkNN readout leaves all of them well below CREST (Table 3, Appendix N), confirming that CREST's advantage stems from the contrastively learned geometry rather than the kkNN predictor.

G4. Reference atlas coverage, scaling, and convex-hull bounds. We agree that retrieval-based prediction cannot extrapolate beyond the convex hull of the reference atlas, and Section 5 now states this limitation more explicitly. The below revisions quantify how much of CREST's performance reflects representation quality versus reference atlas coverage:

  1. Fixed reference atlas scaling (Section 4.5, Figure 3, Appendix P): Keeping the reference atlas fixed across all training sizes, CREST's atlas-based Pearson Δ\Delta correlation still nearly doubles alongside near-linear gains in Condition Retrieval@10, reflecting improvements in representation quality rather than just increased atlas coverage.
  2. Neighbor composition (Appendix O): For held-out queries, we quantified how often the top-1 retrieved atlas profile carries the queried perturbation from another cell line, and measured the Jaccard overlap of top-5050 neighbor sets for the same perturbation across different held-out lines versus distinct perturbations within the same line.
  3. Convex-hull bounds: The Table 3 oracle combines training responses within the same convex hull to reach roughly three times CREST's Pearson Δ\Delta correlation, demonstrating substantial headroom within the existing atlas.

Update on Section 4.6. We thank the reviewers for their constructive feedback and questions regarding dataset diversity, baseline coverage, and single-cell evaluations. During the review period, the ExPert preprint (Schwartz et al., 2026) was released on bioRxiv, concurrent work that independently underscores the practical importance of perturbation retrieval, aligning closely with the candidate prioritization framing in our Introduction (Section 1). Given the opportune timing of this release, we de-prioritized our earlier zero-shot Perturb-seq transfer experiment in favor of directly evaluating CREST on ExPert's multi-context single-cell Perturb-seq inverse retrieval benchmark, which tasks models with ranking candidate CRISPRi perturbations from groups of perturbed cells across unseen cell lines, stimulation states, and human donors. Extending natively to noisy single-cell readouts, CREST significantly outperforms 1212 of 1313 competing baselines across every metric (one-sided Wilcoxon signed-rank test, Holm-corrected p<0.01p < 0.01) and achieves near-parity with ExPert despite training on a smaller corpus. All corresponding updates and methodological details can be found in Section 4.6 and Appendix R.

Thank you for the additional experiments. I think these results are a useful addition. I would like to point out that part of the concerns I have regarding this work is the somewhat strong statement about the novelty of the perturbation retrieval and condition-to-perturbation narrative. This is indeed not novel --as you also highlighted -- so I would change the way this is written in the paper. I went thorught the section and the appendix. I now have a few questions to understand the experimental setting and interpretation of the results:

  1. ** Generalisation setting:** My understanding is that CREST primarily transfers knowledge of perturbations encountered during L1000 training to unseen cellular contexts and assays. Is this also the case for the ExPert benchmark? In particular, how many of the evaluated CRISPRi perturbations were already represented in CREST's training vocabulary?

  2. Baseline comparability: Were the competing methods evaluated using the original ExPert benchmark implementations and training protocols? I am particularly interested in whether they had access to comparable multi-context training information, or whether some were trained on individual datasets and evaluated on unseen contexts.

  3. Retrieval protocol: Could you clarify how CREST was adapted to the inverse-retrieval task, particularly which reference profiles were available at inference? It would also help to understand how you represented the unseen donor and stimulation contexts.

Thank you again for the additional work.

Thank you for the quick reply and comments! Please see the revised manuscript - I had not uploaded the updated manuscript at the time of your most recent response. Thank you again for your time.

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