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Under review as a conference paper at ICLR 2027

On Probability Misallocation in Single-Cell Perturbation Prediction

Abstract

Single-cell perturbation prediction aims to model how interventions reshape cellular populations. Despite substantial progress across diverse modeling paradigms, little is known about the structure of the distributional errors that remain. We uncover a recurring failure across modeling paradigms: models misallocate probability across expression levels, even when mean expression is accurately predicted. We term the shared failure mode probability misallocation. In this work, we systematically characterize where misallocation occurs and show that the error can materially alter the biological conclusions that perturbation prediction is intended to support. Guided by this diagnosis, we propose several simple yet effective corrections that substantially reduce probability misallocation and improve perturbation prediction quality across modeling paradigms and datasets. Further analysis reveals why misallocation persists under existing objectives and how data characteristics shape the supervision required. Together, our work provides a new perspective on single-cell perturbation prediction and practical guidance for building more reliable virtual-cell models to accelerate biological discovery.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
AI for Science, AI for Biology

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_67eCOpenReview ↗
Rating
3
Confidence
3
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

This paper studies single-cell perturbation prediction, which identifies probability misallocation between the learned distribution and the true data distribution: even when the model can predict the mean expression precisely, it can still assign wrong probability mass to different expression levels. The paper separates errors at the zero boundary from errors in the positive-expression region using survival function and KS-based diagnostics. It then evaluates these errors across PBMC, Replogle, and Tahoe100M, using modeling paradigms including Linear, CPA, Squidiff, STATE, and Doloris*. Informed by the diagnostics, the paper proposes 3 correction strategies, including hurdle parameterization, incidence supervision, and multi-threshold supervision. Experiments show that direct probability supervision can reduce probability misallocation, as well as improve metrics on differential expressions and perturbation effects. The paper also analyzes why several learning objectives can still leave probability misallocation, and how the choice of supervision is related to sparsity and error location.

Critical strengths
  1. The paper conducts a systematic empirical analysis to characterize probability misallocation. The experiments are well controlled by using a shared preprocessing, split, and evaluation protocol across several modeling paradigms on 3 datasets. It also compares prediction KS against a real-real reference. This makes the identified failure mode convincing.

  2. The correction experiments reasonably isolated the effect of probability supervision, by keeping the backbone and main training setup fixed.

Critical weaknesses
  1. The analysis does not yet support a general explanation of the failure mechanism across objectives.

Section 5 gives useful mechanism-specific explanations for mean supervision, generative objectives, and distribution matching, but these results have different scopes, with some of them being local diagnostics or counterexamples. Thus, the broader claims about why existing objectives leave probability misallocation should be stated more carefully.

  1. The supervision-choice result does not yet show how to choose a better supervision before testing.

The analyses on sparsity and error location explain the observed difference between incidence and multithreshold supervision, but they are descriptive analyses rather than selection rules. Although this is explicitly acknowledged, a rule that can choose the better supervision before seeing test performance would be appealing.

Questions for authors
  1. Could you clarify which results only show that an objective can leave probability misallocation, and which results support that the objective itself systematically tends to produce this failure?

  2. Could you provide a prospective test of the supervision-choice rule? Based on your findings, do you have any insights on this?

  3. Do you expect incidence or multi-threshold supervision to work similarly for other paradigms such as CellFlow or PerturbDiff, as the correction experiments mainly focus on STATE, Doloris*, and the Gaussian predictor? If this is not tested, should the broader claim be restricted to the model families evaluated with these corrections?

Reviewer_W53bOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
1
Presentation
2
Soundness
2
Read review
Paper summary

The paper shows that single-cell perturbation models often fail to predict the correct gene-expression distributions, even when they predict the mean accurately. The authors study this problem across different models and propose additional training losses to improve predictions.

Critical strengths

The paper studies an important aspect of single-cell perturbation prediction, which is also novel.

Critical weaknesses
  1. The paper shows that probability misallocation can be large, but it is less clear how often it occurs. What fraction of perturbation-gene pairs show substantial misallocation?
  2. In some cases, improvements in probability misallocation come at the cost of lower performance on other metrics. The paper should discuss these trade-offs more clearly.
Questions for authors
  1. The paper is a bit difficult to parse because the notation could be clearer and more consistent. For example, the survival function is sometimes written with subscripts and sometimes without them. Some quantities, such as \mu, are used without being explicitly introduced. I would recommend a paragraph introducing the notation.
  2. Why not consider a negative binomial likelihood directly? The authors propose additional supervision to better match expression distributions. Since negative binomial distributions are commonly used for single-cell RNA-seq counts, how would the approach compare with training a model using a negative binomial or hurdle-negative-binomial likelihood? Could such a model achieve similar improvements without additional probability supervision?
  3. How do the proposed methods perform on the Parse dataset?
  4. Why not include perturbation mean as a baseline? Note that perturb mean copies control cells and applies the average perturbation effect across training contexts. I think since it copies controls, it would preserve much of the original cell-to-cell variability and might reduce probability misallocation without additional supervision.
  5. How are the thresholds selected? How does their placement affect the results and why does increasing the number of thresholds sometimes lead to worse performance?
Reviewer_L2iLOpenReview ↗
Rating
2(+1)
Confidence
4
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

This work characterizes "probability misallocation" across expression levels in single-cell perturbation models, demonstrates its impact on downstream biological conclusions, and introduces simple corrective strategies to improve distributional fidelity across modeling paradigms.

Critical strengths
  • The paper is easy to read.
  • It contains lots of contents to support their idea.
Critical weaknesses
  1. Baseline configurations. The authors removed Doloris’s native BCE sparsity mask (yielding Doloris*), and CPA uses a Gaussian decoder with a truncation adapter rather than its supported NB/ZINB likelihoods. The models that deviate most in Figs. 2–4 are precisely these modified configurations. Furthermore, the paper reports neither the original Doloris nor any NB/ZINB-based baseline.

  2. Questionable baseline results. For example, Squidiff yields an R2R^2 of −218 / −617 / −10.2 (Tables 6–8), which suggests an implementation or scaling error. On PBMC and Tahoe100M, many baselines achieve an AUROC around 0.500, undermining the claim of being “best on 11/14 metrics.”

  3. Confounded attribution for the core result (Gaussian + BCE). The gains cannot be solely attributed to incidence supervision. The “lightweight” model is in fact an 8-component hurdle-lognormal mixture trained with MMD, mean matching, and regularization terms. Its only ablation (Gaussian without BCE) appears to be a failed training run, yielding R2R^2 = 0.898 and AUROC = 0.500 on PBMC.

  4. Alignment bias between evaluation metrics and the training objective. The DE metrics and ES rely on the Wilcoxon test, which is directly driven by incidence (Eqs. D.2–D.3). Supervising incidence will therefore improve these metrics almost by construction. Meanwhile, expression-level metrics show no improvement; for example, the PDCorr of STATE + BCE degrades across all three datasets.

  5. Inconsistent effects of the proposed corrections and overstated claims. Section 4.2.2 states that DE and perturbation-effect metrics improve for both models, yet several results in Table 1 contradict this. For example, on Tahoe100M, the PDS-L1 of Doloris* + BCE drops from 0.875 to 0.641. Additionally, the paper omits standard deviations across random seeds.

others: No code is provided.

Questions for authors
  • How does the original Doloris (with its native BCE sparsity mask) perform, and how does it compare against Doloris* + BCE and Doloris* + MT?

  • Why was CPA evaluated without an NB/ZINB likelihood? Does the misallocation persist with an NB/ZINB decoder or an scVI-style model?

  • Why does Squidiff yield an R2R^2 of −218 / −617?

  • What caused the training failure of the Gaussian model without BCE? Can you provide ablations that individually remove MMD, mean matching, and the mixture components?

  • Do the improvements persist under DE methods that are less sensitive to zeros (e.g., pseudobulk DESeq2/edgeR)?

  • Please report the standard deviations across the three random seeds in Table 1, particularly for ES.

  • The performance drops in Table 1 contradict the claim in Section 4.2.2 that both categories of metrics improve. How do the authors account for this, and will the corresponding statements in the main text be revised?

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