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Under review as a conference paper at ICLR 2027

Program State Distribution Regularization for Learning Across Single Cell Technologies: Benefits and Limitations

Abstract

Single-cell integration aims to enable joint analysis of datasets by reconciling technical distribution shifts while preserving biological variation. Most methods rely on correspondences or invariances across datasets that can be ambiguous, unstable, or absent when biological support set differs across datasets. Methods based on gene programs offer a more structured unit of alignment, but matching program identity alone does not ensure comparable program states or their combinations. We posit the joint distribution of shared program states as the cross technology invariant, and explicitly decompose it into program specific state distributions and interprogram dependence. We implement this decomposition using a shared program bottleneck with inference and observation modules specific to each technology, aligning program marginals through quantiles and interprogram dependence in rank space. Controlled simulations with five independent generators and five optimization repeats show higher correlation between matched factors than the same model without alignment at all four tested levels of observation distortion. On a development cohort, adding dependence alignment improves mean clustering and transfer scores over marginal alignment across five paired fits; for donors excluded during training, prediction of protein from RNA raises median protein from 0.187 without alignment to 0.250 with the combined objective. These results show that aligning program state distributions can improve recovery of shared factors and prediction across technologies.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
single-cell integration, cross-technology learning, gene programs, distribution alignment, Wasserstein barycenter, copula dependence, domain adaptation, representation learning

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_kLqGOpenReview ↗
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Paper summary

This paper studies distribution regularization for learning shared representations across single-cell technologies. A count-reconstruction model combines technology-specific modules with a shared latent bottleneck. Quantile matching aligns coordinate marginals, while a smooth-rank kernel discrepancy aligns inter-coordinate dependence. The method assumes comparable captured biological populations across technologies and uses a soft total-variance penalty to discourage global shrinkage. Experiments examine simulated factor recovery, real-data integration, held-out donor protein prediction, and robustness to population differences. Results indicate task-dependent benefits alongside losses in biological geometry. Separate stability audits and selection-shift experiments identify limitations in interpreting individual coordinates and applying alignment when captured populations differ.

Critical strengths
  1. Separating marginal distributions from inter-coordinate dependence makes the alignment target explicit. Comparing six alignment objectives within the same reconstruction backbone provides useful evidence about their distinct effects and trade-offs.
  2. Independent simulation generators support factor-recovery gains under comparable populations, and confirmation cohorts show clustering improvements. The paper also documents selective-capture failures and unsuccessful factor interpretation, providing meaningful boundaries on the method's applicability.
Critical weaknesses
  1. Shrinking selected coordinates relative to the fixed smooth-rank bandwidth can lower the discrepancy without changing exact ranks, while other coordinates satisfy the total-variance floor. The normalized marginal diagnostics and exact-rank improvements are useful, but do not establish that training avoids this failure mode.
  2. Consistent transfer-F1 gains are not established on the confirmation cohorts, and protein prediction lacks a marginal-only control and site-independent testing. No combined-model factor passes the semantic audit. Unexplained differences between Tables 9 and 13, unavailable reproducibility artifacts, and verified bibliographic errors further weaken confidence in the evidence.
  3. Lots of citation errors. Harmony lists Nathan instead of Nghia Millard; Kunes et al. lists Robert C. instead of Russell Z. Kunes; scETM lists Qianxi instead of Jian Tang; scCRAFT lists Panagiotis instead of Paraskevas Filippidis; and Hrovatin et al. omits Shrey Parikh from an otherwise unabridged author list.
Questions for authors
  1. The fixed-bandwidth smooth-rank loss can decrease when selected coordinates shrink, even if exact-rank dependence is unchanged and the total-variance floor is satisfied. Table 15 normalizes marginal discrepancies but does not isolate this dependence-loss failure mode. Do the downstream gains persist when training prevents coordinate-wise rescaling from reducing the dependence loss?
  2. Table 2 reports improved protein prediction for combined alignment over no alignment, but does not include the marginal-only model. The contribution of dependence matching to this result is therefore unresolved. How much protein-prediction improvement remains over marginal alignment alone under the identical donor split and probe protocol?
  3. Both BMMC test donors come from acquisition site 4, which is also represented in training, and acquisition site defines the model's technical batches. The current result therefore measures donor transfer within a represented site. What evidence supports extending the protein-prediction benefit to an acquisition site excluded from representation and probe training?
  4. Table 5 shows substantial cross-technology cell-type composition differences, while the selective-capture experiments demonstrate that alignment can suppress genuine biological variation. What evidence establishes that the integration gains on the real cohorts preserve biological population differences rather than remove them?
  5. The combined model has mean iLISI of 0.374 in Table 9 and 0.425 in Table 13, although the no-alignment and marginal-only rows agree across tables. The reproducibility package is not yet available. What run-level provenance explains this discrepancy in the reported primary-model results?
2 comments
AuthorsOpenReview ↗

Response to reviewer kLqG: targeted controls, generalization and reproducibility

Thank you for recognizing the controlled comparisons and for identifying specific issues requiring further evidence. We address each question below and distinguish results for the submitted model from later revisions.

Q1 — Does the benefit survive removal of the rescaling shortcut?

Yes, for clustering on the three tested cohorts. We agree that fixed-bandwidth smooth ranks are scale-sensitive and that the total-variance floor does not exclude coordinate-wise shrinkage.

We tested a targeted modification: within each technology, center each coordinate and apply max-absolute prescaling followed by unit-RMS normalization before computing smooth ranks. Only the dependence branch changes; reconstruction and marginal alignment retain the original coordinates. For nonconstant coordinates in exact arithmetic, positive rescaling cannot reduce this dependence loss.

Five paired optimization seeds on fixed splits give: Cohort ARI gain over marginal-only Positive seeds ARI gain over no alignment GSE +0.0644 ± 0.0506 5/5 +0.0467 ± 0.0468 Ding +0.0671 ± 0.0524 5/5 +0.0214 ± 0.0355 Pancreas +0.0599 ± 0.0244 5/5 +0.1032 ± 0.0509

Values are paired mean differences ± sample SD, not biological replication. GSE uses the Table 13 supplementary training implementation. These are endpoint-specific gains: on pancreas, biological ASW and transfer F1 versus marginal-only change by −0.0304 and −0.0153. This intervention shows that clustering gains need not depend on the specified shortcut; it does not prove that the original training never exploited it or exclude constant-coordinate collapse.

Q2 — Protein prediction versus marginal-only alignment

We added the requested comparison under the identical donor split and protein-probe protocol. The combined-minus-marginal median paired per-protein ΔR², averaged over five seeds, is +0.00103 ± 0.01069, positive in 2/5 seeds. Thus, the submitted combined-versus-none result does not establish a stable dependence-specific protein gain. We distinguish whole-representation predictive utility from the incremental contribution of dependence matching.

Q3 — Transfer to an excluded acquisition site

The submitted experiment tests new donors at a represented site. In an additional experiment, all site-4 cells were excluded from source feature selection, representation training and probe training. Unseen-site inference used a new, fixed equal-weight ensemble of source encoders, without target-RNA calibration.

Combined-minus-none median paired ΔR² is +0.00570 ± 0.00762 over five seeds, positive in 4/5; the donor-specific mean differences are +0.01347 and approximately zero. Combined-minus-marginal is +0.00411 ± 0.01447, positive in 3/5. These provide limited evidence for one excluded site under this additional inference protocol, not general native unseen-site capability.

Q4 — Preservation of biological population differences

We do not infer biological preservation from improved mixing. As clarified in revised Section 5.1 and Appendix B.6, the assumption concerns latent program-state distributions. Different cell-type proportions need not change every program's marginal, but can change background-associated programs and the joint distribution. The submitted objective does not automatically identify invariant programs or solve population mismatch.

We retain the negative selection-shift results and the 0/64 semantic-audit outcome. Stable biological program discovery and uniform transfer-F1 gains are not claimed. Applicability requires sampling metadata and independent biological evidence; alignment itself cannot certify that genuine population differences were preserved.

Q5 — Table 9/Table 13 provenance

The combined rows use separate checkpoint sets from the primary and supplementary training implementations. Five-seed reruns reproduce their respective mean iLISI values, 0.373691 and 0.424604. They are not two summaries of identical checkpoints.

A seed-7 intervention replacing the supplementary loss assembly with the primary expression reproduces Table 9's iLISI of 0.399365 rather than Table 13's 0.410314. This identifies a concrete implementation sensitivity in that run; we do not claim that the single-seed intervention establishes the complete mechanism across all seeds. We acknowledge that the original presentation did not adequately distinguish these runsets.

Bibliography and reproducibility

The revised bibliography corrects Nghia Millard, Russell Z. Kunes, Jian Tang and Paraskevas Filippidis, and includes Shrey Parikh. We apologize for these author-metadata errors.

The revision now includes the anonymous repository link. This supplies the project address; we do not equate providing a link with independently verified reproduction of every experiment.

AuthorsOpenReview ↗

How much of a known population difference survives alignment?

We added a real-cell experiment that measures the loss of a known composition difference directly. We imposed a 38.75-percentage-point difference in CD4 T-cell prevalence between Chromium and Quartz-Seq2 using CD4 T and HEK cells from GSE133549. Across five fits on the same split, a cross-technology classifier recovered 24.5 points without alignment, 16.2 with program-wise marginal alignment alone, and 14.6 with full PSDR. Over the same comparisons, same-type cross-technology MMD² improved from 0.493 to 0.209 to 0.173. Thus, most of the additional attenuation relative to the unaligned fit was already present with marginal alignment alone.

Full PSDR-C recovered 14.3 points. The loss was visible in a specific population: the classifier correctly identified 77.5% of held-out Quartz-Seq2 HEK cells, compared with 92.5% without alignment. The held-out RNA supported the distinction between the two groups. CD3D was detected in 90% of annotated CD4 T cells and 2.5% of HEK cells, while KRT18 was detected in 5% and 90%, respectively. Holding the fitted PSDR-C scores and backgrounds fixed, the final calibration changed the recovered gap only from 14.6 to 14.3 points. Most of the attenuation in the full model therefore preceded that step.

For Q4, the five-seed result qualifies the integration claim: alignment improved same-type agreement while making a genuine prevalence difference less recoverable. The aggregate integration gains on the observational cohorts cannot by themselves establish preservation of their population differences (revised Appendix F.13, Table 25).

Reviewer_urSKOpenReview ↗
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Paper summary

The paper studies how to make single-cell RNA data from different sequencing technologies comparable. It trains an autoencoder on raw counts, with a shared latent space and technology-specific input and output layers. It adds a penalty that makes the distribution of the latent coordinates the same in every technology. The penalty has two parts. One matches each coordinate's distribution separately, through quantiles. The other matches how coordinates vary together, through ranks. The justification is an explicit assumption that all technologies capture the same population of cell states.

The main findings are that in simulations where this assumption holds, the penalty improves recovery of the true factors over the same model without it, at some cost in local neighborhood structure. For example, factor correlation rises from 0.671 to 0.714 at the strongest distortion. Also, on the development cohort, adding the dependence part to the per-coordinate part improves clustering (ARI 0.258 → 0.301) and label prediction. On two further cohorts, the full penalty improves ARI over no alignment.

Critical strengths
  • Combining single-cell data from different technologies is a routine need.

  • The paper is explicit in what it assumes. Assumptions 1–2 separate per-coordinate distributions from dependence. Eq. 3 matches marginals through 1-D W2W_2 to a reference-free quantile barycenter, and Eq. 4 matches dependence through MMD on ranks.

  • The ablation isolates the alignment target. The key experiment changes only the loss and keeps the model fixed. E3 compares six objectives on one frozen backbone with five paired seeds. This separates the effect of the target from the effect of the architecture, which comparisons across methods cannot do.

  • Ablation is fair, the paper deliberately breaks its own assumption and reports the negative results. RQ4 shows the gain reverses under selective capture and that dependence alignment suppresses a genuine dependence difference (l.404). The paper keeps representation utility separate from factor interpretation (l.397–401).

Critical weaknesses
  • Im not sure how this method differs from batch-effect correction. The model is an autoencoder with batch-specific layers and a penalty that makes the latent distribution the same in every batch. "Technology" is just the batch label: inDrop batches in pancreas (l.840) and collection sites in BMMC (l.843–844). Matching each coordinate and their dependence together is the same as matching the full distribution (l.194–195), which existing methods already do. Examples are MMD between batches (MMD-ResNet, Shaham et al., 2017) and LIGER's quantile alignment of factor loadings, the closest match to the quantile loss. Related Work cites LIGER only for program correspondences (l.068–069) and discusses no single-cell method that matches distributions (l.076–083). The "program" framing does not set the method apart, since none of the 64 factors passes the paper's own test (l.321–322). Please explain the difference, and add LIGER with its alignment step as a baseline.

  • The paper does not address the best-known failure of distribution matching. When technologies capture different mixes of cell states, forcing their distributions to match merges cells that should stay apart. The method assumes this away (l.144–151), even though the abstract faults earlier methods for breaking in exactly this case (l.014–016). This failure is well documented (Hrovatin et al., cited at l.077; Zhao et al., ICML 2019), and BERMUDA (Wang et al., 2019) and uniPort (Cao et al., 2022) were built to handle it. RQ4 rediscovers it without this context (l.375–376), and the unbalanced-transport variant does not fix it (l.378–379). The paper's own cohorts already differ in cell-type mix by up to 0.39 in total variation (Table 5). Please relate RQ4 to this work, and explain how a user can tell when the method is safe to use.

  • The one new element, as far as I can see, splitting the penalty into a per-coordinate part and a dependence part, is never shown to beat matching the full distribution directly. The headline comparison is against the per-coordinate part alone, the weakest variant (l.026–028, l.258–261). Against MMD on the full latent space with the same model (Table 1), results are within noise and split across metrics: ARI 0.301 ± 0.023 vs. 0.288 ± 0.017, and Bio ASW 0.592 vs. 0.613. The only clear gain is on the rank distance that the dependence loss itself optimizes (l.200–201). This test is run only on the development cohort used to set the configuration (l.232–233). Against existing methods, scCRAFT and DRVI have higher ARI on all three cohorts (Tables 9–10), and the protein result in the abstract has no integration baseline (Table 2).

Questions for authors

I think a more clear "novelty" statement is required.

3 comments
AuthorsOpenReview ↗

Comment 1 to Reviewer urSK: Response to Critical Weakness 1

Thank you for the opportunity to clarify the novelty of our method and how it differs from full-MMD and LIGER.

Explanation of the term “technology”

Yes, our method is a batch-effect correction method. We distinguish two components of batch effects. Differences in sample composition reflect which biological states are sampled and in what proportions. Technical variation in measurement refers to differences in how technologies measure the same biological state. We use “technology” to emphasize that our goal is to correct this technical variation while preserving sample composition in the representation or/and corrected data used for downstream tasks.

Explanation of the term “program”

Gene program has several established uses in single-cell biology. These studies illustrate the data-driven use in our work.

StudyWhat it calls a gene program
Marmarelis et al., Communications BiologyNMF factors
Kotliar et al., Nature MethodscNMF-derived factors
Lotfollahi et al., Nature Cell BiologyPredefined gene sets and newly learned programs

We use “program” for a learned multigene factor with decoder-defined gene responses. Single-gene measurements can be too variable for reliable alignment. The results of Experiment 5 limit the biological interpretation of individual factors. The integration and prediction experiments evaluate the learned representation.

Comparison of alignment targets in our method, full-MMD, and LIGER

Our program-wise target differs from those of full-MMD and LIGER. A program's biological state distribution can be shared even when joint cell states differ. The table compares the targets, conditions for forced distortion, and sufficient sample sizes for a given binned total variation error.

SymbolMeaning
PtP_tScore law in batch tt
PrP_rScore law in batch rr
S^k\widehat S_kCell score kk
S^\widehat{\mathbf S}A cell's score vector
KKNumber of scores
C=cC=cMatched LIGER cluster
Γk=γ\Gamma_k=\gammaBiological context for program kk
Δ\DeltaBiological gap on a common scale
nnCells drawn per batch
nCn_CMin. cells per cluster
nΓn_\GammaMin. cells per program–context pair
JJMatched cluster count
HHProgram–context pair count
pCp_CMin. cluster probability
pΓp_\GammaMin. program–context probability

Group minima span both batches.

For DD histograms per batch, at most ss bins each, b(s,D)=⌈(slog⁡2+log⁡(8D/δ))/(2η2)⌉b(s,D)=\lceil(s\log2+\log(8D/\delta))/(2\eta^2)\rceil. For groups of probability at least p>0p>0, N(b,p,j)=max⁡2b,8log⁡(4j/δ)/pN(b,p,j)=\max\\{2b,8\log(4j/\delta)\\}/p suffices for jj groups. LL is the number of bins per score. Both batches attain total variation error at most η\eta with probability at least 1−δ1-\delta under fixed scoring functions, bins, and groups with independent cells (Appendix B.5).

MethodAlignment targetCondition for forced distortionSufficient cells per groupSufficient draws per batch
Full-MMDPt(S^)↔Pr(S^)P_t(\widehat{\mathbf S})\leftrightarrow P_r(\widehat{\mathbf S})Δjoint>ε\Delta_{\rm joint} > \varepsilonn≥b(LK,1)n\ge b(L^K,1)n≥b(LK,1)n\ge b(L^K,1)
LIGERPt(S^k∣C=c)↔Pr(S^k∣C=c)P_t(\widehat S_k\mid C=c)\leftrightarrow P_r(\widehat S_k\mid C=c)Δk∣c>ε\Delta_{k\mid c} > \varepsilonnC≥b(L,KJ)n_C\ge b(L,KJ)n≥N(b(L,KJ),pC,J)n\ge N(b(L,KJ),p_C,J)
Program-wise, Eq. (3)Pt(S^k)↔Pr(S^k)P_t(\widehat S_k)\leftrightarrow P_r(\widehat S_k)Δk>ε\Delta_k > \varepsilonn≥b(L,K)n\ge b(L,K)n≥b(L,K)n\ge b(L,K)
Proposed, fixed contextsPt(S^k∣Γk=γ)↔Pr(S^k∣Γk=γ)P_t(\widehat S_k\mid\Gamma_k=\gamma)\leftrightarrow P_r(\widehat S_k\mid\Gamma_k=\gamma)Δk∣γ>ε\Delta_{k\mid\gamma} > \varepsilonnΓ≥b(L,H)n_\Gamma\ge b(L,H)n≥N(b(L,H),pΓ,H)n\ge N(b(L,H),p_\Gamma,H)

If the corrected distributions are within ε\varepsilon on the same scale and under the same metric, at least one differs from its biological law by (Δ−ε)/2(\Delta-\varepsilon)/2 or more (Appendix B.6). With a shared biological state distribution and continuous, strictly increasing measurements of that state, equal percentiles give the two readings of the same state, Qr,k=mr,k∘mt,k−1∘Qt,kQ_{r,k}=m_{r,k}\circ m_{t,k}^{-1}\circ Q_{t,k} (Theorem 1, Section 4.3). The LKL^K count concerns a joint histogram. The fixed-kernel MMD value has a separate concentration bound (Appendix B.5).

Our contribution is separate control of program-wise and dependence constraints during count-model training. For continuous marginals, equality of population marginals and joint rank distributions implies equality of the joint score distributions (Appendix B.2). The 128-point quantile grid in Eq. (3) and the smooth ranks in Eq. (4) approximate these constraints.

LIGER as a baseline

We have added LIGER with its native quantileNorm alignment as a baseline (Appendix F.9). Our method achieves a higher aggregate scIB score on all three cohorts (Tables 2–3).

AuthorsOpenReview ↗

Comment 2 to Reviewer urSK: Response to Critical Weakness 2

Thank you for pointing out the risk of overcorrection when sample compositions differ and for sharing the relevant references. As discussed in Comment 1, differences in sample composition are also a central concern of our work. In addition to the scIB biological conservation metrics in Table 2, we tested how much of a known composition difference PSDR and PSDR-C preserve while reducing technical differences. PSDR-C compares program-wise distributions within backgrounds covered by both technologies (Eq. 7 in Section 4 and Appendix C.5 of the revision). In this stress test, PSDR reduced same-type cross-technology differences and recovered more of the known composition gap than full-MMD and uniPort, with LIGER recovering the largest gap.

Using Chromium and Quartz-Seq2 cells from GSE133549, we set the training proportions of CD4 T and HEK cells so that the CD4 T-cell proportions differed by 38.75 percentage points, comparable to the difference you highlighted. This extends RQ4 to real cells and includes uniPort, which you cited. We evaluated all methods on the same held-out cells. The table reports the initial three paired seeds (7, 19, and 37). Appendix F.13 gives the protocol and the five-seed extension. Lower same-type cross-technology MMD² indicates that cells of the same type have more similar representations across technologies. We estimate the recovered CD4 T-cell proportion gap by reweighting held-out cross-technology classification results to the known proportions. Values closer to +38.75 are better. The within-technology opposite-label neighbor rate measures how often cells from the two types are neighbors within the same technology.

MethodSame-type cross-technology MMD² ↓Recovered CD4 T-cell proportion gap (pp, closer to +38.75 is better)Within-technology opposite-label neighbor rate ↓Cross-technology label transfer balanced accuracy ↑
No alignment0.471+24.710.46%93.13%
PSDR (without joint-rank alignment)0.167+22.910.94%92.50%
PSDR (full)0.134+18.912.07%91.04%
PSDR-C (without joint-rank alignment)0.127+14.811.03%89.58%
PSDR-C (full)0.119+16.011.81%90.00%
full-MMD0.122+16.610.97%90.21%
LIGER (with native quantile alignment)0.165+28.110.08%94.38%
uniPort0.178−32.210.92%73.54%

PSDR reduced technical differences and attenuated the known composition difference. Relative to no alignment, the program-wise term alone reduced the recovered gap by 1.7 percentage points. Adding joint-rank alignment reduced it by a further 4.0 percentage points and increased the within-technology opposite-label neighbor rate. Full PSDR recovered a gap between those of full-MMD and LIGER. LIGER's native quantile alignment left the held-out representations unchanged in this experiment.

PSDR-C further reduced same-type cross-technology differences, and overcorrection persisted in this setting. Full PSDR-C reduced MMD² to 0.119 and recovered a gap of 16.0 percentage points. Removing joint-rank alignment gave an average of 14.8 percentage points, with effects in both directions across seeds. In a frozen-model comparison for full PSDR-C, the final calibration step reduced MMD² from 0.134 to 0.119 and left the recovered gap unchanged in all three seeds. The reduction in the recoverable composition difference was already present before final calibration.

Checks before alignment

  • PSDR. Use sample and capture metadata or independent measurements to check whether the biological program-state distributions are comparable across the full set of retained cells in each technology.
  • PSDR-C. Check that both technologies cover the relevant biological backgrounds and that states are comparable within each background. For example, use paired samples or independent measurements to check subtype or activation-state distributions within a cell type. The proportions of the shared backgrounds may differ.
  • Joint-rank alignment (both versions). Enable this term when the biological patterns of program co-activity are comparable across the retained populations.

On held-out data, compare with no alignment to check that same-type cross-technology differences decrease and known biological differences are preserved (Section 6 and Appendices B.7 and F.13).

AuthorsOpenReview ↗

Comment 3 to Reviewer urSK: Response to Critical Weakness 3

Thank you for pointing out the need for more direct evidence of the benefits of our alignment objective and for integration baselines in the protein prediction experiment. We have expanded the baseline comparisons in the experimental section. By overall scIB₈ score, PSDR-C ranks among the leading distribution alignment methods and is competitive across the full set of integration baselines (Tables 2 and 11).

In Comment 1, we compared the alignment targets of PSDR, full-MMD, and LIGER. The original PSDR compares each program's distribution across all retained cells in a batch. When sample composition changes, a program's overall distribution can differ even if its biological state distribution is shared within the same biological context. This motivated PSDR-C. For a biological context Bk=bB_k=b covered by both technologies tt and rr, PSDR-C compares the quantiles of program kk at the same level uu, Qtk(u∣b)↔Qrk(u∣b)Q_{tk}(u\mid b)\leftrightarrow Q_{rk}(u\mid b) (Section 4, Eq. 7 and Appendix C.5).

To assess performance on additional datasets, we kept our configuration fixed and added comparisons with other distribution alignment methods on Ding PBMC and pancreas. The table below is excerpted from the main integration results (Tables 2 and 11).

MethodGSE133549 scIB₈ ↑Ding PBMC scIB₈ ↑Pancreas scIB₈ ↑
PSDR0.67000.67370.7578
PSDR-C0.72000.68720.7622
full-MMD0.66950.64350.7448
LIGER (with native quantile alignment)0.63820.64900.6420
uniPort0.71750.64090.8023

Bold indicates the highest score among the methods shown in each column.

The original PSDR improved clustering on both Ding PBMC and pancreas. Compared with no alignment, mean ARI increased by 0.055 and 0.112, respectively (Table 12). In the same-backbone comparison with full-MMD across five paired runs, the corresponding gains were 0.033 and 0.052 (Appendix F.8).

PSDR-C achieved higher scIB₈ scores than full-MMD and LIGER on all three datasets. Compared with uniPort, PSDR-C scored higher on Ding PBMC and lower on pancreas. Across the five paired GSE133549 runs, their mean scores differed by 0.0025 in favor of PSDR-C.

You also noted that the protein prediction result in the abstract lacked integration baselines. We added these comparisons using the original BMMC donor split and the same RNA-to-protein prediction protocol. The median protein R2R^2, averaged over five fits for each method, was 0.250 (original PSDR), 0.227 (PSDR-C), 0.131 (scVI), 0.199 (DRVI), and 0.207 (scCRAFT) (Table 20 and Appendix F.8).

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Paper summary

This paper proposes a regularization approach for learning shared single-cell representations across technologies. It aligns both the marginal distributions of latent program activities and their dependence structure, using quantile matching and rank-based MMD within a count-reconstruction model. Experiments examine factor recovery, data integration, protein prediction, and failures under population differences. The results show useful but task-dependent improvements.

Critical strengths
  1. The paper investigates how to align biological program distributions across single-cell technologies, an important question that deserves greater attention. Its analysis of both the benefits and limitations provides useful insights for future work.

  2. Same-backbone comparisons isolate the effects of different alignment objectives, while simulations assess recovery against known biological factors.

  3. The paper explicitly investigates selective capture, missing states, and genuine biological differences. It also distinguishes useful representations from interpretable biological programs.

Critical weaknesses
  1. None of the 64 combined-model factors passes the joint semantic audit. Consequently, the evidence supports representation utility more strongly than stable biological program discovery.

  2. The method assumes that the cell populations being aligned have the same mix of biological states. This may not be true in practice, and the method provides no way to check, using only the data, whether alignment is appropriate.

Questions for authors

What practical checks or experimental metadata would help users decide whether the population-comparability assumption is reasonable?

2 comments
AuthorsOpenReview ↗

Scope of the contribution and when to align program states

Thank you for recognizing the controlled comparisons and the analysis of population shifts.

CW1: Stable biological program discovery. We agree with your interpretation. None of the 64 factors passes the joint semantic audit, so the evidence supports the utility of the representation more strongly than the interpretation of individual factors. Our contribution is to formulate program-state distribution regularization and study its effects on cross-technology representation learning. Stable biological program discovery is outside the scope of that contribution. The revised draft retains the 0/64 result and explicitly limits the abstract’s factor-recovery claim to controlled simulations.

CW2 and Question: When is alignment appropriate? The revised Introduction states the assumption at the level of latent program-state distributions. Different cell-type proportions can leave a program’s marginal distribution unchanged if its state distribution is the same across the cell backgrounds whose proportions shift. For programs that vary across those backgrounds, composition can change the marginal. The joint objective also requires comparable dependence across programs.

Unpaired RNA counts alone generally cannot distinguish a change in how a state is measured from a change in which states were captured. The most informative evidence comes from matched donors and conditions measured across technologies, randomized aliquots, and records of sorting, capture, and filtering. Independent cell annotations or protein measurements can reveal missing populations and within-type differences. We also recommend comparing the intended biological endpoint with a no-alignment baseline, alongside batch mixing. Known missing states or genuine differences in program-state prevalence are reasons to avoid unconditional matching of the affected distributions. The revised draft gives these checks in the Discussion and derives the program-level conditions in Appendix B.6.

AuthorsOpenReview ↗

A held-out check for population comparability

Your question prompted us to test whether a check on held-out cells could reveal overcorrection. We used real CD4 T and HEK cells from GSE133549 and set the CD4 T-cell prevalence to 69.375% in Chromium and 30.625% in Quartz-Seq2. This gave us a known biological difference of 38.75 percentage points. On the same held-out cells, we measured both the cross-technology discrepancy within each cell type and the prevalence gap recoverable by a cross-technology classifier. We estimated the latter by reweighting the classifier’s held-out confusion matrix to the known proportions.

Across five fits on a fixed split, same-type MMD² fell from 0.493 without alignment to 0.173 with PSDR and 0.146 with PSDR-C. Yet the recoverable prevalence gap also fell, from 24.5 points without alignment to 14.6 with PSDR and 14.3 with PSDR-C. The unaligned result matters here because the classifier recovered only part of the known gap even before correction.

This gives users a practical check when independent annotations or mixture proportions are available. On held-out cells, measure agreement within the annotated groups and ask how much of a known between-sample difference remains recoverable relative to an unaligned fit. In this experiment, the second measurement revealed a loss that the first alone would have missed (revised Appendix F.13, Table 25).

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

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