- Rating
- 3(+1)
- Confidence
- 2
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 3(+1)
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Paper summary
The paper studies PCA when data come from several batches that share the same factor loading space but have different means, and the batch label is known for only of the samples. It combines two covariance estimates, , where is computed from the labelled samples centred within each batch and from the unlabelled samples centred globally.
Using random matrix theory, the authors define a "safe" set of weights for which the differences between batch means do not create extra spikes outside the noise bulk. They estimate the strength of these differences from the labelled data and choose the safe weight closest to . Theorems 1–3 show that this choice recovers the correct number of factors, minimizes the detection threshold and the subspace error over the safe set, and matches oracle PCA when is safe.
The method is validated by simulations () and on two sci-Plex A549 single-cell RNA subsets (Nutlin-3a and Pirarubicin).
Critical strengths
S1. The paper addresses a practical problem with careful theory. Batch effects can dominate the leading principal components, and throwing away the unlabelled samples wastes data. The method uses the partial labels to estimate how strong the batch differences are (Eq. 5) and then chooses one weight automatically, without cross-validation. Theorem 2 shows that this weight minimizes the detection threshold over the safe set and matches oracle PCA when is safe, which directly answers the question the paper asks. I find this a principled and simple rule for a common situation.
S2. The results agree with the theory. In Fig. 1 the error drops sharply at the edge of the safe region, and the selected weight is close to the lowest error and to the oracle. On Nutlin-3a, the natural weight keeps about 37 components against about 10 for the proposed weight, which fits the explanation of spurious batch directions. The proposed method also has the highest held-out variance efficiency on both datasets (0.505 against 0.431 and 0.339 on Nutlin-3a; 0.450 against 0.372 and 0.277 on Pirarubicin). Code and data are provided.
Critical weaknesses
W1. The experiments are too narrow to support the practical claims.
The simulations use a single configuration: four equal batches, three factors with fixed strengths along the first coordinates (), , and in every case. I would like to see unequal batches, small , more or weaker factors, heteroscedastic noise and some misspecification. In the simulations only different weights of the same method and the oracle are compared, with no outside method.
On the real data, only one competitor from the literature is used (mean-shift PCA, Li et al. 2026), and both datasets come from a single cell line and experiment. Simpler ways of using the labels are not compared either, for example projecting out the estimated batch-mean directions, or predicting the missing labels and centring within the predicted batches. The appendix contains proofs but no additional experiments.
Without broader evidence, I find it hard to judge whether the method is useful beyond the tested setting.
W2. Some key formulas are not explained in the main text, and the assumptions do not fit the application well.
At L142–143 a weight is called safe when , but the reason is not given there. only gets its meaning later (L222–225), as the level above which a spike from the unlabelled part separates from the noise bulk. Similarly, the estimator of in Eq. (5), the edge equation (6), the bulk-edge estimate (9) and the component rule (10) are given without derivation; their justification appears only inside the appendix proofs (Lemma 1) and at L199–201. Algorithm 1 also appears (L147) before the quantities it uses are defined.
On the application side, the theory assumes noise with equal variance, while log-normalized scRNA-seq data are strongly heteroscedastic. The asymptotics assume many labelled samples, but the real data use about 20 labelled cells (3–5 per batch) with thousands of genes. The theory reveals labels at random, while the experiments reveal 10% within each batch (L362).
As a result, readers cannot easily follow or check the method, and the real-data results may not reflect the conditions the theory needs.
Questions for authors
Q1. Why is safety defined as ? Could you give the intuition in Section 2?
Q2. How are Eqs. (5), (6), (9) and (10) obtained? Please explain them briefly or point to where each is justified.
Q3. This question is very important for my assessment. Do you claim to be the first to use a factor model with a shared loading space and batch-specific intercepts? If not, why are no other methods compared in the simulations?
Q4. Apart from mean-shift PCA (Li et al. 2026), are there other methods that could be compared on the real data?
Q5. This is a suggestion, and the answer could change my assessment. How does the method compare with projecting out the estimated batch-mean directions, or with predicting the missing labels and then centring within batches?
Q6. For the revision, could you add more simulation settings (unequal batches, small , more or weaker factors, heteroscedastic noise) and at least one more real dataset, even in the appendix?
Minor: in Table 1 the methods are compared at very different numbers of components (about 3 to 37). The p53 test uses nominal without multiple-testing correction. The error formula of Theorem 3 is not checked by any simulation.
6 comments
Author response (Part 2/2)
Continuation of Part 1.
Q6: Additional simulations and an independent real dataset
Thank you for these suggestions. We have added simulations with unequal population sizes, labeling proportions of 5%–15%, more and weaker factors, and heteroscedastic noise. These labeling proportions correspond to 40–120 labeled observations across 10 populations. We also include mean-shift PCA (Li et al., 2026) and PCA after mean projection (Haghighatkhah et al., 2022) as additional baselines in these simulations. Weighted hybrid PCA achieves the lowest average factor loading space estimation error in all reported settings (Appendix B.2, Tables 5–6, lines 1514–1557 of the revised manuscript).
We have also added an experiment on the Quartet RNA dataset (Yu et al., 2024). This dataset contains measurements of four biological reference materials across 11 batches. We use partially observed batch labels for estimation and material identities only for evaluation. We use the SNR metric introduced by Yu et al. (2024) to assess material separation after projection onto the PCs selected by each method. Weighted hybrid PCA achieves the highest average SNR among the compared methods, close to that of fully labeled oracle PCA (Section 4.3 and Table 2, lines 459–495 of the revised manuscript).
Q3: Novelty and relation to existing factor models
Related factor models use fully observed population memberships to estimate shared factor loadings while modeling intercept differences (De Roover, 2021) or population-specific factors (De Vito et al., 2019). McNicholas (2010) also studies related factor models for semi-supervised classification, with the aim of predicting unknown population memberships. We study semi-supervised PCA for estimating the shared factor loading space, treating population-specific intercept differences as nuisance variation. We have clarified these distinctions in the Introduction (lines 112–118 of the revised manuscript).
Consider the Quartet RNA example (Yu et al., 2024) discussed in Q6. Differences between materials represent biological information of interest, whereas differences between batches are nuisance effects. In this example, classification methods such as McNicholas (2010) model biological differences between materials for classification. Our method models differences between batches to extract biological information despite these nuisance effects. We therefore do not include these classification methods as direct baselines for evaluating shared factor loading space estimation.
Q4 and Q5: Additional baselines
Thank you for suggesting these additional baseline methods. As explained in Q3, those factor models and semi-supervised classification methods are not suitable direct baselines for our setting. Mean-shift PCA (Li et al., 2026) treats between-population mean differences as nuisance variation. It aims to recover the underlying covariance structure. This makes it a suitable baseline for our problem. We have also included PCA after mean projection (Haghighatkhah et al., 2022) as a baseline in the revised simulations and real-data experiments.
We have not included prediction of missing batch labels followed by within-batch centering. In our experiments, simple classifiers produced highly unstable predictions of these labels, especially at low labeling proportions. Addressing this instability would require further methodological work beyond a straightforward baseline implementation.
Minor comments
Following Reviewer 1’s suggestion, we revised the noise-scale estimator as permitted by our theory. This leads to more conservative PC selection, especially under the natural weight. We have updated the experiments. Across methods, the mean PC counts are 1.42–5.95 for Nutlin-3a and 1.14–4.17 for Pirarubicin (Table 1, lines 433–446 of the revised manuscript). Weighted hybrid PCA retains its performance advantage on both datasets. As expected, excluding additional PCs caused by between-population mean differences leads to fewer selected PCs.
For the p53 association tests, we have adopted Benjamini–Hochberg-adjusted p-values to account for multiple testing (lines 1568–1570 of the revised manuscript).
We have added simulations comparing the empirical error with the theoretical value in Theorem 3 (Section 4.1 and Figure 2, lines 371–393 of the revised manuscript). Figure 2 shows that the empirical error approaches the theoretical value as the sample size increases.
Thank you for the revision; three short follow-up questions
Thank you for the detailed response and the substantial revision. I checked the revised paper. The new simulations in Appendix B.2 (5–15% labels, unequal populations, more and weaker factors, heteroscedastic noise, and the mean-shift and mean-projection baselines), the Quartet RNA experiment with an oracle reference (Table 2), the check of Theorem 3 (Figure 2), the paired comparisons (Tables 3, 4 and 7), the Benjamini–Hochberg correction, and the new explanations in Section 2 and in the Introduction address my main concerns. I am inclined to raise my rating, and I would first like to see your answers to the three short questions below.
Q1. The noise estimator also includes the variance of the factors and of the batch-mean differences, so it overestimates for finite . How large is this bias on the single-cell data, for example compared with the labeled estimator corrected for the lost degrees of freedom? It may explain why the selected numbers of components dropped so much (for example to 1.42 for labeled PCA on Nutlin-3a).
Q2. In Table 1 all methods find about one p53-associated component, and Table 7 shows a paired difference in count of only 0.09 and 0.05. The higher proportion therefore comes mainly from selecting fewer components. I suggest describing the p53 result in this way, rather than as more p53 signal being recovered. Similarly, on the Quartet data the SNR of weighted hybrid PCA (35.6 ± 2.7 dB) is close to that of labeled PCA (34.6 ± 2.1 dB), while the gain in distance to the oracle space is clear.
Q3. You mention that predicting the missing labels and then centring within the predicted batches gave very unstable results. Reporting these results briefly in the appendix would show why this simple approach is not enough.
Author response (Part 1/2)
Thank you for your careful reading and constructive suggestions. Below, we address the comments and describe the corresponding revisions, including additional experiments.
W1: Experiments too narrow to support practical claims
Thank you for your suggestions on the experiments. We have expanded the simulations and added an independent real dataset. These additions are described in our response to Q6. Our response to Q4 and Q5 explains the choice of baselines and describes the additional baselines included in the revised experiments.
W2: Explanation of formulas and dependence on assumptions
Thank you for suggesting these clarifications. Our intention was to explain the population quantities and their roles in the algorithm before presenting the estimation formulas. Algorithm 1 provides an overview of the procedure. We have expanded these explanations in Section 2 (lines 153–158 of the revised manuscript). We have also added references to the relevant theory and proofs alongside the corresponding formulas (lines 175, 185, 199, and 205–206 of the revised manuscript).
We have added simulations with heteroscedastic noise to assess robustness beyond the equal-variance assumption, as described in Q6.
In the real-data experiments, we select labeled observations randomly within each batch to ensure that all batches are represented. Conditional on population memberships, labeling is independent of factor scores and noise. With the same labeling proportion across batches, the labeled and unlabeled samples retain the same limiting mixing proportions. These properties allow the conditional arguments in our proofs to extend to this labeling scheme.
We assess performance at labeling proportions of 5%–15% through the additional simulations described in our response to Q6. This range includes the 10% labeling proportion used in our single-cell RNA experiments.
Q1: Intuition for the safety condition
Selecting the number of PCs using the spectral edge, as in Eq. (10), is an established approach (Kritchman and Nadler, 2008). In the limit, the spectral edge gives the upper bound for eigenvalues generated by noise alone. In contrast, detectable factors produce eigenvalues above this edge.
However, between-population mean differences can also produce eigenvalues above the spectral edge. Here, γμ estimates the strength of these mean differences. After weighting, their estimated strength becomes (1−α)γμ. Our theory gives a threshold for this contribution, estimated by tα. Eq. (7) defines a weight as safe when (1−α)γμ≤tα. This prevents mean differences from generating additional eigenvalues above the spectral edge in the limit.
We have clarified the role of this threshold and the safety condition in Section 2 (lines 153–158 of the revised manuscript).
Q2: Derivation of Eq. (5), (6), (9), and (10)
We briefly explain the derivation and justification of each formula in turn.
Eq. (5) estimates the strength of the between-population mean differences. We estimate the population means and mixing proportions from the labeled observations. The correction term accounts for noise in the estimated means. Lemma 1 establishes the consistency of the resulting estimator.
We solve Eq. (6) for sα. It estimates sα, the quantity used to calculate the spectral edge. The population equation for sα follows from Eq. (11). We set the derivative of its right-hand side to zero at the spectral edge. We then replace the parameters with their sample counterparts to obtain Eq. (6).
Eq. (9) estimates the spectral edge. We obtain it by substituting sα into the sample counterpart of Eq. (11).
Eq. (10) applies the spectral edge criterion discussed in Q1. The added 1/logp term accounts for fluctuations around the estimated edge. Theorem 1 provides the theoretical justification for this selection rule.
Continued in Part 2.