acceptodds
Under review as a conference paper at ICLR 2027

CRNDiff: Count-Native Diffusion Framework via Chemical Reaction Networks

Abstract

Scientific measurements such as single-cell RNA (scRNA) sequencing often take the form of nonnegative integer counts, whereas continuous-state diffusion models approximate this discrete structure using continuous coordinates. Building on stochastic chemical reaction networks (CRNs), a class of count-native Markov jump processes, we introduce CRNDiff, a structured framework that combines count-space diffusion with inference-time conditioning on rare subpopulations. An independent birth–death instantiation yields a closed-form transition kernel for forward noising. This kernel enables reverse sampling via forward-filtering backward-sampling (FFBS) and supports data-driven selection of the terminal noising time, eliminating the need for a validation sweep. This tractability also lets us introduce tilted Feynman–Kac (FK) steering, a method for sampling target subpopulations from a frozen generator without retraining. By tilting posterior marginals before FK particle correction, steering mitigates importance-weight concentration when the target population is rare. Using scRNA-seq data from the human heart cell atlas, we test the ability of CRNDiff to generate cell-type-specific distributions. Across the three evaluated target populations, CRNDiff achieves the highest conditional fidelity among the evaluated generative models, with larger mean purity margins for rarer target populations. Generated cells preserve marker-level differential-expression structure. Replacing real training cells for the target classes with generated cells yields downstream classification performance approaching that of the real-data reference.

Primary area:
generative models
Keywords:
Generative diffusion models, Chemical reaction network, Count-native generative modeling, Single-cell RNA sequencing

Reviews

Among:
Shape:
1234this paper, Top 4%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.33 over 3 reviews, above 96% of the others.
Reviewer_z7bwOpenReview ↗
Rating
3(+1)
Confidence
3(+1)
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

The authors present CRNDiff, a count-native diffusion framework whose forward noising process is defined by stochastic chemical reaction networks, aimed at integer data such as scRNA-seq. With an independent birth-death network, the forward kernel is closed-form (Binomial plus Poisson), enabling exact forward-filtering backward-sampling with a learned posterior and a data-driven terminal noising time based on excess-covariance decay. For conditional generation from a frozen generator, they propose tilted Feynman-Kac steering, which combines per-gene marginal tilting with discriminator-weighted particle correction. Empirical results on synthetic data and the human heart cell atlas suggest higher conditional fidelity than scVI, scANVI, CFGen, and MDLM, especially for rarer cell types, along with preserved marker structure and strong downstream classification utility.

Critical strengths

I personally enjoyed the paper. I find the math very elegant and interesting, especially the use of chemical reaction networks to define a count-native forward process with a closed-form kernel, which makes exact reverse sampling possible. The paper is overall well written: concise but thorough, and the authors are open about the limits of their choices. There are multiple aspects I appreciated, one of which is the attention to devise a forward process that destroys not only single-gene overdispersion but also correlated structure across genes, and the use of this to pick the terminal noising time in a principled way rather than by a validation sweep. Overall, the presented method seems to fit single-cell data very well and in a creative way.

Critical weaknesses

For now, I gave a weak reject based on my questions below, but I am more than happy to reconsider upon rebuttal. I think the main flaw of this submission is that the results section feel a little slim. I am open to increase my score and excited to engage with the authors during the rebuttal phase.

  1. In my opinion, the motivation presented in the introduction is a bit slim. What is the gap in the literature? What's the problem with latent models with a negative binomial decoder? And with the other discrete approaches?
  2. Minor, I would add the word "discrete" somewhere in section 2.1's title.
  3. Minor, L88 define ff.
  4. Minor (notation): ss denotes an earlier forward time in Eqs. (4)–(5) (s<ts < t), but is reused as the reverse-time variable in Eq. (2) (s∈[0,T]s \in [0, T], forward time T−sT - s), with the opposite meaning. A distinct symbol would avoid confusion.
  5. I got a bit confused by the notation inconsistency in (9). What's the difference between the S\mathbb{S} matrix and its bold counterpart S\boldsymbol{S}.
  6. Please, correct me if I am wrong, but the conditioning pipeline relies on several estimated components. I am wondering about the accuracy of each of them. (i) The marginal tilt uses per-gene count histograms (unit bins over 0–512) from a limited number of target cells (e.g., 3,168 neuronal). Due to overdispersion, these histograms are heavily skewed toward zero with long, sparsely populated tails, so for higher counts, precisely where target-specific expression is expected, the empirical densities are near zero and the ratio is largely determined by sampling noise and by the smoothing and clipping constants. Moreover, the per-target τ\tau is chosen without a stated procedure. (ii) The FK correction is exact only for the true density ratio (Eq. 23), but it is approximated by the odds of a gradient-boosted classifier on 256 selected genes, used without an upper clip and without a reported calibration check. Given that a conditionally fine-tuned generator outperforms tilted FK on all fidelity metrics (Table 10), the practical benefit of this pipeline over conditional training should be better justified.
  7. As far as I could understand, the evaluation does not directly assess sparsity, a defining feature of scRNA-seq counts. Table 9 reports only the coefficient of variation of detected-gene counts, not their mean, nor the per-gene or per-cell fraction of zeros. Since the stationary distribution is product-Poisson and the generator is reported as underdispersed (median Fano 2.403 vs. 2.953), comparing zero fractions (e.g., per-gene zero proportion vs. mean expression) between generated and real cells would clarify whether CRNDiff reproduces the sparsity structure of the data.
  8. I am concerned about possible over-concentration of generated cells for rare targets. For neuronal cells, tilted FK outputs descend from only ~4.5% of initial particles (Anc. 0.045, i.e., ~110 ancestors for 2,500 cells; Table 7). High output uniqueness (0.995) shows that cells are not exact copies, but not that they cover the target's variability, and the reported metrics (per-gene W1, MMD², PCC of means) are not designed to detect concentration. Moreover, UMAP (Fig. 7) does not preserve spread, and the atlas-level PCA (Figs. 6, 8) is dominated by between-cell-type axes. I suggest a PCA fitted on the real target population only, with a comparison of per-PC and total variance between generated and real cells.
  9. The evaluation on the heart atlas is thorough, combining distributional, marker-level, and downstream metrics with extensive ablations. However, it is limited to a single dataset, with three target populations among eleven classes, the rarest of which (neuronal) still comprises ~2% of cells. It would strengthen the paper to also report results on standard single-cell generation benchmarks, such as those used by CFGen (Palma et al., 2025) and scLDM (Palla et al., 2026), e.g., Dentate Gyrus, Tabula Muris (123 cell types), and HLCA (50 cell types). These would show how tilted FK steering behaves with many, and considerably rarer, cell types and more complex target distributions. The diversity-sensitive metrics reported there (1-NN accuracy, precision/recall) would also help address the concentration concern raised above.
  10. In Fig. 7d, a substantial fraction of generated neuronal cells appears to lie outside the main neuronal cluster of the test cells (Fig. 7a), notably in a dense group within a different cluster, despite a CellTypist purity of 0.971. This raises the question of whether the marginal tilt steers generation toward neuronal-like per-gene distributions in a region shared with other cell types, rather than into the neuronal population itself. Could the authors show an overlay of real and generated neuronal cells in the same embedding, report which neuronal subtypes (or CellTypist labels) the generated cells are assigned to, and quantify the fraction of generated cells whose nearest real neighbors are neuronal?
Questions for authors
  1. Might be a naive question, what happens if one sets V>1V>1? Was the choice dictated by simplicity?
  2. How should τ\tau be chosen in practice? Too large a value amplifies noise in the estimated per-gene ratios and degrades fidelity (Table 8, τ=1\tau=1), while too small a value leaves the FK correction to do all the work, reintroducing the weight concentration the tilt is meant to avoid. The best value between 0.2 and 0.4 is target- and metric-dependent. Could the authors provide a selection procedure or criterion that does not require test-set access, for instance based on ESS or genealogical diversity?
  3. How do runtime and efficiency compare to continuous approaches?
7 comments
AuthorsOpenReview ↗

Response to Reviewer z7bw (1/5)

z7bw-W0: For now, I gave a weak reject based on my questions below, but I am more than happy to reconsider upon rebuttal. …

We are very grateful for this thorough and generous review, for the kind words about the mathematics, and for the reviewer's openness to revisiting the score after the rebuttal. The detailed suggestions shaped most of the new analyses in the revision. Following your suggestions, we have substantially extended the results: a second atlas with much rarer targets, a count-native baseline, coverage for all methods, and analyses of each component of the conditioning pipeline. We respond to each point below.

z7bw-W1: In my opinion, the motivation presented in the introduction is a bit slim. What is the gap in the literature? What's the problem with latent models with a negative binomial decoder? And with the other discrete approaches?

Thank you; we agree that the motivation needed to be more specific. The introduction has been rewritten along these three questions.

  • Gap: generating rare or newly defined populations without retraining; existing conditional generators need training-time labels.

  • NB latent models (scVI, scANVI, CFGen): gene dependence passes through a low-dimensional latent; conditioning needs training-time labels.

  • Other discrete models: categorical diffusion (MDLM) ignores count order; count-native models (CountsDiff and others) condition only on training-time labels. We now compare directly with CountsDiff: CRNDiff is better on 12 of 15 heart target–metric pairs (Table 2) and on both lung targets, where CountsDiff rarely generates the target (Table 3).

The data motivate a count-native model: 94.1% zeros, 56.9% of nonzero entries equal one (Table 4).

z7bw-W2: Minor, I would add the word “discrete” somewhere in section 2.1's title.

Thank you. Section 2.1 is now titled “Continuous-time discrete-state diffusion models”.

z7bw-W3: Minor, L88 define f.

Thank you. f is now defined where the generator L is introduced, as a bounded test function f:X→Rf:\mathcal X\to\mathbb R, so that ∂tE[f(Xt)]=E[(Lf)(Xt)]\partial_t\mathbb E[f(X_t)]=\mathbb E[(Lf)(X_t)].

z7bw-W4: Minor (notation): s denotes an earlier forward time in Eqs. (4)–(5) (s < t), but is reused as the reverse-time variable in Eq. (2) (s ∈ [0,T], forward time T-s), with the opposite meaning. A distinct symbol would avoid confusion.

Thank you for pointing this out. The reverse-time variable is now u ∈ [0,T] (Eq. 2), so s keeps a single meaning, an earlier forward time with s < t.

z7bw-W5: I got a bit confused by the notation inconsistency in (9). What's the difference between the 𝕊 matrix and its bold counterpart S.

Thank you. 𝕊 and S denoted the same object, the stoichiometric matrix whose columns give the change in counts caused by each reaction; the bold version was a typesetting inconsistency. All stoichiometric matrices are now written in blackboard bold, which also distinguishes them from S, the number of species (Section 2.2).

AuthorsOpenReview ↗

Response to Reviewer z7bw (2/5)

z7bw-W6: Please, correct me if I am wrong, but the conditioning pipeline relies on several estimated components. …

Thank you for this careful analysis of each estimated component. We address them in turn.

1. Noise in the ratio tables (point i). We agree that the high-count tails of the histograms are estimated from few cells. The following two investigations show that this noise has little effect on the generated cells.

First, we rebuilt the neuronal ratio tables from random subsets of the target cells, keeping the generator, discriminator and sampler fixed. Even with 10% of the cells (317 instead of 3,168), the results stay close to those with all cells (Table 14; one frozen generator, one sampling seed, test split): purity 0.969 vs. 0.986, W1 0.060 vs. 0.065, MMD² 0.0119 vs. 0.0131 and coverage 0.812 vs. 0.785.

Second, tilting only the 32 genes with the strongest tilt and leaving the other 1,968 genes untilted gives the same fidelity and coverage as tilting all genes (W1 0.063 vs. 0.063, coverage 0.791 vs. 0.791, purity 0.971 vs. 0.984). The effect of the tilt is therefore concentrated in a few genes, so the noisy tables of the remaining genes contribute little, and the exponent τ < 1 further tempers the ratios. The smoothing constant (ε = 0.5/N) and the clipping range (±log 1000) are now listed in Table 5.

Both investigations are reported in Table 14 (Appendix B.7).

2. Choice of τ (point i). In the revision, we explicitly state a procedure that uses validation cells only (Appendix B.6, Eqs. 45–46). For each candidate τ ∈ {0.2,…,1.0}, we normalize W1, MMD², purity and coverage so that 1 equals the real-cell value, cap the scores at 1, and select the τ closest to the all-ones vector. This gives 0.4, 0.2 and 0.2 for the heart targets and 0.2 and 0.4 for the lung targets. Figure 11 shows how the four scores change with τ.

3. Calibration and clipping of the discriminator (point ii). On held-out cells not used for fitting, the discriminators separate target from proposal cells well and are close to calibrated (Table 11). AUC is the probability that a target cell scores higher than a proposal cell (1: perfect, 0.5: chance); ECE is the expected calibration error after correcting for class proportions (0: perfect); the last column is the share of the total weight carried by the largest 1% of odds. Their definitions are given in Appendix B.6.

TargetAUCECEWeight carried by the top 1% of odds
Endothelial0.9310.06015%
Myeloid0.9880.02841%
Neuronal0.9920.01176%

As the reviewer anticipated, the odds become heavy-tailed for rare targets: for neuronal cells, 1% of the particles carry three quarters of the weight, which explains the genealogical concentration in Table 12. We therefore tested an upper clip at the median odds of held-out real target cells. Its effect is inconsistent across the three generators (test split, unclipped / clipped): W1 0.063 / 0.060, 0.063 / 0.070, 0.070 / 0.063; MMD² 0.0135 / 0.0116, 0.0118 / 0.0167, 0.0167 / 0.0115. We therefore keep the odds unclipped and report this result in Appendix B.6.

4. Benefit over conditional training (point ii). We agree that conditional fine-tuning gives better fidelity when labels are plentiful, and the revised Section 5.2 now states this. Steering a frozen generator is useful in three settings that the revision now evaluates:

  • Few labels (Table 15). With 10% of the neuronal labels (317 cells), fine-tuning yields mostly non-neuronal cells, whereas steering, with ratio tables and discriminator built from the same cells, stays close to its full-label performance: purity 0.959 vs. 0.984 and coverage 0.782 vs. 0.791, whereas fine-tuning reaches 0.359 and 0.256.

  • A target without a training label (Table 16). Steering to UAP1⁺ endothelial cells, defined by a marker gene after training, yields 99.9% UAP1⁺ cells, whereas only 8.6% of endothelial cells express UAP1; label-conditioned generators such as scVI, scANVI, CFGen and CountsDiff could not target this subset without new labels and retraining, whereas CRNDiff reaches it by steering the same frozen generator.

  • Cost (Table 19). Adapting to a new target takes 0.18 h instead of 4.8 h of fine-tuning and leaves the generator unchanged; in exchange, sampling is slower (205 s vs. 31 s per 1,000 cells).

AuthorsOpenReview ↗

Response to Reviewer z7bw (3/5)

z7bw-W7: As far as I could understand, the evaluation does not directly assess sparsity, a defining feature of scRNA-seq counts. …

Thank you for this suggestion; sparsity is indeed a defining feature of the data, and the original evaluation did not assess it directly. The new Appendix B.8 reports, for all methods and targets, the zero fraction, library size, median Fano factor and variance (Table 18), and the zero fraction against mean expression per gene (Figure 13).

Zero fractions. For endothelial and myeloid cells, CRNDiff reproduces the per-cell zero fraction (0.924 vs. 0.922, 0.927 vs. 0.919), and its gene-wise zero fractions follow those of real cells across expression levels (Figure 13). For neuronal cells, CRNDiff overestimates the overall zero fraction (0.959 vs. 0.949) but, at a given mean, underestimates it for highly expressed genes. Both deviations follow from the count statistics: smaller generated library sizes lower the mean expression of most genes and introduce excess zeros overall, whereas reduced count overdispersion decreases the zero rate at any fixed mean.

Dispersion. The Fano factors quoted by the reviewer (2.403 vs. 2.953) refer to the unconditional pool. For the conditionally generated cells, the median per-gene Fano factor is close to that of real cells (1.59, 1.52, 1.38 vs. 1.53, 1.61, 1.49 for endothelial, myeloid and neuronal cells) and the closest among all methods for endothelial and myeloid cells.

Library size. This analysis revealed a limitation: CRNDiff cells have smaller library sizes than real cells (495 vs. 612, 524 vs. 779, 164 vs. 244). Comparing with cells of the same type in the unconditional samples (Table 17) locates the deficit: for myeloid cells it is already present in the generator, whereas for endothelial and neuronal cells it arises during steering. CountsDiff, which also generates counts directly, shows a similar deficit, while scVI, scANVI and CFGen draw library sizes from real cells and match them by construction. We discuss this limitation in Section 6.

z7bw-W8: I am concerned about possible over-concentration of generated cells for rare targets. …

Thank you for raising this important point and for the concrete suggestion. We followed the suggestion: we analyzed variance of generated cells along a PCA fitted on real target cells (Table 18) and coverage for all methods (Tables 2, 3). The variance ratio of CRNDiff is comparable to that of the best baseline for endothelial and myeloid cells (0.89 vs. 0.92 and 0.81 vs. 0.79, both MDLM) but lower for neuronal cells (0.63 vs. 0.82, CFGen; Table 18). The concentration is real for the rarest target. To locate its source, we compared samplers on the reference generator (neuronal, test split, three sampling seeds; this additional analysis is summarized qualitatively in Appendix B.8):

SamplerVariance ratioPurity
Tilted FK, τ = 0.2 (selected)0.600.98
FK only (no tilt)0.560.99
Tilt only (no FK)0.940.06
Tilted FK, τ = 10.99lower

Three observations locate the source. First, the tilt does not cause the concentration: FK steering without the tilt is at least as concentrated as tilted FK steering (variance ratio 0.56 vs. 0.60), whereas the tilt alone keeps the variance close to that of real cells (0.94) but produces mostly non-neuronal cells (purity 0.06). Second, the concentration comes from the FK correction itself: the discriminator odds are heavy-tailed for rare targets (the top 1% of neuronal odds carry 76% of the weight), so the output descends from few initial particles (4.5% for neuronal cells). Using more particles does not remove this concentration. The particles are the candidate cells that the FK sampler propagates and resamples in parallel during generation (5,000 by default; Algorithm 2). On validation cells, four times as many particles more than doubled the number of distinct initial particles from which the output cells descend, but did not increase the variance of the generated cells. The limitation therefore lies in the concentrated weights, not in the number of particles. Third, a larger τ restores variance at the cost of purity and fidelity; at τ = 1 the variance reaches the real value only because library sizes are inflated about fourfold. Appendix B.8 discusses this source, Figure 12 shows the effect of τ on the variance, and the Discussion states the limitation; covering the internal variability of rare targets while keeping high purity is an important direction for future work.

Reviewer_jvM6OpenReview ↗
Rating
4
Confidence
3
Informativeness
3
Presentation
3
Soundness
3
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Paper summary

This manuscript proposes a diffusion model for (non-negative) discrete count data. The proposed model, CRNDiff, builds on chemical reaction network (also called stochastic Petri nets, etc.) framework that effectively corresponds to a continuous-time (discrete-state) Markov process, where states correspond to discrete-valued configuration of the reaction network system and state transitions are defined by the associated reaction network hazards.

CRNDiff uses an independent birth-death process for which analytical solution for the forward noising process is developed in this work. The noising process eventually converges to the product of independent Poissons. The reverse process can be sampled using FFBS, where the intractable kernel Q is approximated by a trainable neural net model.

The amount of noising (in the underlying continuous-time system) is determined by analysing reduction in correlations across dimensions and deviations from dimension-wise independent Poisson model using a second-order calibration criterion between the model and random finite-sample fluctuations.

Authors propose conditional generation using a two-stage guidance that involves marginal tilting of the posterior and an additional classifier-based guidance or correction.

Method description starts with a compact but comprehensive and clear description of continuous-time Markov chains and chemical reaction networks.

Method description is super-clear, enjoyable to read. All technical details that I had time to check seem correct.

Method is evaluated and compared against other generative models on a toy dataset and heart cell scRNA-seq data, where it achieves the highest generative performance while preserving biological information, such as differentially expressed genes. Authors also carry out several ablations to demonstrate that guidance needs both marginal tilting and classifier-based guidance. All experiments demonstrate good performance relative to commonly used and strong baselines.

Critical strengths

The main strength of this manuscript is that it develops discrete-state diffusion model using the chemical reaction network formalism and the associated continuous-time Markov chain formalism, together with conditional generation using marginal tilting and classifier based guidance. Method development is careful and comprehensive throughout, and is done from the first principles.

Critical weaknesses

No critical weaknesses.

Questions for authors

Marginal tilting: could the tilting-based guidance be implemented in high-dimensional setting with a small number of tilting coordinates/marginals (e.g, only a small number of genes from \mathcal{D}_{R,i})?

Notational inconsistency in Equation 9: \mathbb{S} vs \mathbf{S}, and \mathbf{n} vs n

Additional baseline/ablation experiments: you could also train a conditional generative model for the three classes/cell types directly. How would that compare against your tilted FK guidance?

Manuscript contains empirical evaluations using one toy dataset and one scRNA-seq dataset. Having more empirical and more complex evaluations would make the results more convincing. For example, in the context of scRNA-seq data, generation of peripheral blood mononuclear cells (PBMCs) with significantly more cell types than 3.

Authors should comment of applicability and scalability to higher dimensional and structured data (e.g. images).

3 comments
AuthorsOpenReview ↗

Response to Reviewer jvM6 (1/2)

To Reviewer jvM6. We sincerely thank the reviewer for the very positive assessment and for the careful reading of the method. We are glad that the derivations and their presentation came across clearly. The reviewer's questions were very valuable: they led to the top-k tilting experiment, to a direct comparison with conditional training in the settings where steering matters, and to the second atlas.

jvM6-Q1: Marginal tilting: could the tilting-based guidance be implemented in high-dimensional setting with a small number of tilting coordinates/marginals (e.g, only a small number of genes from DR,i\mathcal{D}_{R,i})?

Thank you for this insightful suggestion. Yes. We kept the tilt only for the k genes with the strongest tilt and left the rest to the FK correction (neuronal target, one frozen generator, test split, three sampling seeds; discriminator refitted; Table 14, lower block).

The table below shows how the number of tilted genes affects performance:

All 2,000 genesk = 32k = 128
Purity0.9840.9710.983
W10.0630.0630.068
MMD²0.01350.01240.0154
Coverage0.7910.7910.769

Tilting 1.6% of the genes matches tilting all of them in fidelity and coverage, with slightly lower purity, so the cost of the tilt need not grow with dimension. This experiment is now included in Appendix B.7.

jvM6-Q2: Notational inconsistency in Equation 9: 𝕊 vs S, and n vs n

Thank you for spotting this. 𝕊 and S denoted the same stoichiometric matrix; the bold version was a typesetting inconsistency. The input, output and net stoichiometric matrices are now written in blackboard bold throughout, which also distinguishes them from the number of species S, and the state is consistently the bold vector n (Section 2.2).

jvM6-Q3: Additional baseline/ablation experiments: you could also train a conditional generative model for the three classes/cell types directly. How would that compare against your tilted FK guidance?

Thank you for suggesting this comparison; it helped us state more clearly when steering a frozen generator is useful. This comparison is the fine-tuned generator in Table 13. With plentiful labels, fine-tuning gives better fidelity, which Section 5.2 now states. Steering a frozen generator helps where conditional training does not:

  • Few labels (Table 15): with 10% of the neuronal labels, steering keeps a purity of 0.959 and a coverage of 0.782, close to its full-label values (0.984 and 0.791), whereas conditional fine-tuning drops to 0.359 and 0.256.

  • Target without a training label (Table 16): steering to UAP1⁺ endothelial cells yields 99.9% UAP1⁺ cells, versus 8.6% among endothelial cells.

  • Cost (Table 19): a new target takes 0.18 h instead of 4.8 h of fine-tuning, but sampling is slower (205 s vs. 31 s per 1,000 cells).

jvM6-Q4: Manuscript contains empirical evaluations using one toy dataset and one scRNA-seq dataset. …

Thank you; we agree that a second dataset makes the results more convincing. We added a result for the Human Lung Cell Atlas (585k cells, 50 cell types; Section 5.3, Appendix C), also requested by Reviewer z7bw, with two targets much rarer than any heart target, and compared our method with CFGen (public checkpoint), CountsDiff, scANVI and scVI (three seeds, test split; Table 3):

Plasma cell (0.30%)Ionocyte (0.10%)
MethodPurityCoveragePurityCoverage
CRNDiff0.9670.3440.8330.444
CFGen0.9520.1760.4680.266
CountsDiff0.3230.0980.0060.131
scANVI0.3050.0910.0150.124
scVI0.5080.0760.5940.371

Marker genes confirm the identity of generated ionocytes (Figure 15), and an ablation (Table 20) shows that the FK correction is needed for both targets, while the tilt adds most for ionocytes, which the untilted generator almost never produces.

AuthorsOpenReview ↗

Response to Reviewer jvM6 (2/2)

jvM6-Q5: Authors should comment of applicability and scalability to higher dimensional and structured data (e.g. images).

Thank you for this question.

Applicability. Any non-negative integer data can be modelled, including images. Pixel values, however, are quantized intensities rather than counts of sampled molecules, so they may lack the Poisson-like sampling noise that motivates count-native modelling. Natural extensions would be other count-valued omics (Discussion).

Scalability. The forward kernel factorises, so its cost is linear in dimension; the reverse network costs as a standard diffusion model, with memory growing with the count cap; tilting only 32 of the 2,000 genes gives the same fidelity and coverage as tilting all genes, so the cost of the tilt need not grow with dimension. Our method therefore scales well in these respects; its main limitation is that steered sampling is about seven times slower than sampling a conditionally trained generator (Table 19).

Thank you again for your support and for the constructive suggestions.

I want to thank authors for clarifications and additional experiments. I will keep my score, and support acceptance of this manuscript.

Reviewer_Pzw7OpenReview ↗
Rating
3(+2)
Confidence
3
Informativeness
2
Presentation
1
Soundness
1
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Paper summary

This paper presents a new method for doing diffusion on integer data, based on stochastic chemical reaction networks.

Critical strengths

There are some interesting combinations of ideas presented.

Critical weaknesses

It is not clear that the method that they present solves any real problem. They begin their argument about a difference between discrete and continuous space, but continuous space diffusion was shown to be a large-population limit of discrete space diffusion by https://proceedings.iclr.cc/paper_files/paper/2026/hash/45d5823950cab9a88e10c6e8dbff351c-Abstract-Conference.html Meaning that this is not a real problem.

The paper does not empirically compare against the other count-native diffusion models such as Blackout Diffusion, CountsDiff, JUMP, Count Bridges and Count-FM, so we have no way of knowing whether this method presents an improvement

This paper is also very poorly written and structured, making it more difficult for the reader to understand what the point of their method is.

Questions for authors

What gap in existing methods does your approach address? How much does your method improve upon existing methods, and in what way does it do so?

4 comments
AuthorsOpenReview ↗

Response to Reviewer Pzw7 (1/2)

To Reviewer Pzw7. We thank the reviewer for the time spent on our submission and for noting that the paper combines interesting ideas. The comments led us to state the problem and our contribution much more directly in the revision. Below we respond to each point.

Pzw7-W1: It is not clear that the method that they present solves any real problem. They begin their argument about a difference between discrete and continuous space, but continuous space diffusion was shown to be a large-population limit of discrete space diffusion …

We thank the reviewer for pointing us to this work. The cited result, that continuous diffusion is the large-population limit of discrete diffusion, is consistent with our framework; Appendix A.5 derives this limit for CRNs. Single-cell counts, however, are far from that limit: 94.1% of entries are zero and 56.9% of nonzero entries equal one (new Table 4). Our setting is therefore the discrete regime, where a Gaussian approximation of unit jumps is inaccurate, so modelling on the integer lattice is a substantive choice.

More importantly, the discrete–continuous distinction is not our main claim. The problem we solve is generating cells of rare populations on demand from a frozen generator, including populations defined after training. CRNDiff achieves the highest target purity (the fraction of generated cells that a classifier assigns to the target) among the compared methods on all five targets in two atlases (Tables 2 and 3), with the largest margin on the rarest target, ionocytes (0.833 vs. 0.594 for the best baseline). Reviewer z7bw likewise noted that the method “seems to fit single-cell data very well”, and Reviewer jvM6 mentioned that “all experiments demonstrate good performance relative to commonly used and strong baselines”. We therefore believe that our work addresses a real problem.

Pzw7-W2: The paper does not empirically compare against the other count-native diffusion models such as Blackout Diffusion, CountsDiff, JUMP, Count Bridges and Count-FM, so we have no way of knowing whether this method presents an improvement

Thank you for this suggestion, which made the comparison considerably stronger. We added CountsDiff, the count-native model applicable to conditional single-cell generation, to every table (same splits, backbone, count cap and training budget; three training seeds; Tables 2 and 3):

TargetMethodPurity ↑W1 ↓MMD² ↓PCC ↑Coverage ↑
Endothelial (heart)CRNDiff0.9060.0640.00110.9980.820
CountsDiff0.8930.0650.00370.9970.538
Myeloid (heart)CRNDiff0.8860.1100.00320.9870.576
CountsDiff0.8030.1780.00330.9880.360
Neuronal (heart)CRNDiff0.9710.0510.01020.9560.826
CountsDiff0.9390.0550.00980.9610.713
Plasma cell (lung)CRNDiff0.9672.5060.02740.9490.344
CountsDiff0.3233.9730.17330.7440.098
Ionocyte (lung)CRNDiff0.8330.3220.05780.8780.444
CountsDiff0.0060.3770.11720.6860.131

Here, coverage is the fraction of real target cells that have a generated cell among their nearest neighbours. CRNDiff outperforms CountsDiff on 12 of 15 heart target–metric pairs (the other three differ by less than one standard deviation) and on all lung pairs. The remaining models have no conditioning mechanism (Blackout Diffusion, JUMP), no released whole-cell conditional setup (Count Bridges), or are concurrent preprints (Count-FM); adapting them would evaluate our own modifications rather than the published methods. All of them, like CountsDiff, could at most condition on training-time labels, which is the limitation that CRNDiff removes.

Pzw7-W3: This paper is also very poorly written and structured, making it more difficult for the reader to understand what the point of their method is.

We thank the reviewer for this feedback. The other two reviewers found our paper clear (presentation 3; “super-clear, enjoyable to read”, jvM6; “overall well written: concise but thorough”, z7bw), but we take the concern seriously and, following the reviewer's suggestion, have restructured the introduction to state the problem first (rare and post-hoc targets without retraining), then the limitations of existing models and our approach, and added a Discussion with limitations.

AuthorsOpenReview ↗

Response to Reviewer Pzw7 (2/2)

Pzw7-Q1: What gap in existing methods does your approach address? How much does your method improve upon existing methods, and in what way does it do so?

Thank you for this question, which helped us sharpen the introduction.

Gap. Existing conditional generators (scVI, scANVI, CFGen, CountsDiff) need target labels at training time, so a rare, poorly labelled or newly defined population requires retraining. CRNDiff resolves this problem by steering one frozen unconditional generator at sampling time.

Improvement. CRNDiff has the highest target purity on all five targets (Tables 2 and 3), with the largest margin on the rarest target, ionocytes (0.10% of training cells; 0.833 vs. 0.594 for the best baseline, scVI). With 10% of the neuronal labels, our steering keeps a purity of 0.959 whereas standard conditional fine-tuning drops to 0.359 (Table 15); a target without a training label is reached without retraining (Table 16).

We hope that the revision makes the problem and our contribution clearer, and we would welcome any further feedback.

Reviewer_Pzw7OpenReview ↗

Weakness addressed: score increased

Dear Authors, thank you for addressing my concerns. I appreciate your further explanation of the context, clarifying edits to the text, and the additional comparisons against other methods. I raise my score.

Thank you very much for your positive feedback and for raising your score. We truly appreciate your constructive comments, which have helped us improve the clarity and the empirical evaluation of our work.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General response to all reviewers

We thank all three reviewers for their time and their careful, constructive comments, which have substantially improved the paper. Figure, table and appendix numbers refer to the revised PDF, in which new and changed text is shown in blue.

Main revisions are as follows:

  1. Second atlas. The Human Lung Cell Atlas, with two rare targets, plasma cells (0.30% of training cells) and ionocytes (0.10% of training cells), is added (Section 5.3, Appendix C).

  2. Count-native baseline. Comparison with CountsDiff is added to all tables on both atlases.

  3. Diversity. Coverage is now reported for all methods, together with variance along a target-only PCA, sparsity and library sizes (Appendix B.8).

  4. Choice of τ. Selection criterion on validation cells is explicitly described (Appendix B.6).

  5. Conditioning pipeline. We added analyses of the sensitivity of the ratio tables (Table 14), discriminator calibration (Table 11), steering versus conditional fine-tuning with few labels (Table 15), a target without a training label (Table 16), runtime (Table 19).

  6. Cell identity. We included an overlay of real and generated cells in the UMAP embedding (Figure 7), nearest-neighbour fractions (Table 6) and subtype composition (Figure 8) on the heart atlas; marker genes, a steering ablation and library sizes on the lung atlas (Figure 15, Tables 20 and 22).

  7. Presentation. The introduction is restructured around the problem, the notation is fixed, and a Discussion with limitations is added.

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