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Under review as a conference paper at ICLR 2027

SIGCell: Sketched Isotropic Gaussianization of Cell Tokens for Transferable Cytometry Set Encoder

Abstract

Cytometry measures dozens of protein markers on hundreds of thousands of single cells in a blood sample and is a standard tool for profiling the human immune system. However, even with the same marker panel, cytometry data varies greatly across institutions, so a model trained at one institution does not transfer smoothly to another. Existing pretrained cytometry encoders have largely been evaluated within the data they were trained on, or fine-tuned anew with labels for each downstream dataset, so whether a frozen encoder transfers to another institution remains open. We introduce a cell-SIGReg loss term that improves the transferability of set encoders, and present SIGCell (Sketched Isotropic Gaussianized Cell set encoder), a transferable cytometry set encoder trained with it. We identify a sample-context bias in masked set encoders: a cell's token depends strongly on which sample it is encoded with, which is associated with poor transfer of source-fitted cell-type read-outs across samples and institutions. Cell-SIGReg applies the sketched isotropic Gaussian regularizer to the cell tokens pooled over a mini-batch of samples, penalizing the separating structure between samples. We benchmark SIGCell against other pretrained cytometry encoders and classical baseline algorithms. On external datasets, SIGCell improves COVID-19 severity grading (balanced accuracy , against at most for the other frozen representations) and transfers a source-fitted COVID-19 detection rule across institutions without target-cohort labels (AUROC and on two external datasets, first among ten models). Ablations and token-level analyses show that the gain is associated with a much weaker sample-context bias: the share of cell-token variance that lies between samples falls from – to –. Cell-level latent regularization is thus a simple way to improve cross-institution transfer in cytometry set encoders.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
cytometry foundation model, set representation learning, self-supervised learning, immunology, biology, single-cell, cross-institution transfer

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
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Paper summary

The paper asks whether a frozen, self-supervised cytometry set encoder can transfer across institutions without target labels. It identifies a sample-context bias in masked set encoders such as MAESTRO: each cell token is computed in the context of its sample's other cells, but only the pooled sample embedding is supervised, so tokens become sample-specific. Without the proposed term, .93–.98 of token variance lies between samples, versus .10–.19 for the raw markers, and re-encoding the same cells within another sample moves their tokens by about 6–9 times their cell-to-cell spread; the bias is already present at random initialization. SIGCell adds cell-SIGReg on top of masked-set reconstruction and sample-level SIGReg. Cell-SIGReg applies the SIGReg isotropic-Gaussian (Epps–Pulley) statistic to a batch-normalized 64-d projection of cell tokens pooled across the 12 samples of a mini-batch. Proposition 1 argues that, at its target, this caps the between-sample share of variance at about (S−G)/d(S-G)/d without using sample identities. Validation uses one 1,872-sample pretraining corpus and two external COVID-19 cohorts (92 and 124 samples), all on the same 30-marker panel. SIGCell matches MAESTRO in distribution (13-class BA .789 vs .791) and gives the best external severity grading among frozen representations (BA .501, against at most .441). Its source-fitted COVID-19 detection rule transfers with the threshold unchanged at AUROC .949 and .995, first among ten models. A controlled 2×2 ablation shows that the cell term lowers the between-sample share to .12–.24 and raises cell-type read-out on unseen cohorts from .13–.19 to .64–.69 BA, while its benefit to the sample-level read-outs appears only together with sample-SIGReg.

Critical strengths

The paper turns a vague trust in frozen embeddings into a concrete, measurable failure mode, and then shows that a label-free term removes it. It is not only that a new regularizer improves a benchmark: the authors first establish that masked set encoders write the sample into every cell token, demonstrate this both with a variance decomposition and with an intervention that holds the probed cells fixed and changes only their context, show that the bias is already present at initialization, and show that it appears in an independently designed encoder but not in one that attends across cells while being trained differently. That chain of evidence is what makes the diagnosis credible, and the diagnosis should matter beyond cytometry, since the same structural problem applies to any encoder that supervises only a pooled representation of tokens produced in context. The monotone response of the token geometry to the weight of the new term then ties the diagnosis to the proposed fix. The transfer protocol is careful in ways that are unusual in this literature. All baselines are retrained on the same corpus, panel and budget, splits are donor-grouped, the decision threshold is fixed before the external data are opened, and no target label is used for fitting or recalibration. Each baseline is adapted in its own regime and every deviation from its published recipe is documented, while healthy-only and within-gate analyses rule out case mix as the source of the institutional shift. Negative results are also reported rather than buried. Frozen cross-institution evaluation is scarce here, so a protocol this explicit is itself a contribution: it is what allows Table 2 to be read as a comparison of whole models rather than of adaptation tricks.

Critical weaknesses

The sample-level claims rest on a single pretraining run per model and on very small external cohorts. Every model, including all four ablation conditions, is pretrained once at a single seed, so the reported standard deviations describe probe and split variation only and say nothing about variation in the learned representation. The headline severity margin over the next-best frozen representation (.501±.032 against .441±.046) is of the same order as those split SDs, and no paired interval is reported for it. The interaction term of +.141 is computed from four single runs. The cell-weight sweep is notably non-monotone at the sample level: Geanon source-fitted balanced accuracy is .742 / .553 / .710 / .871 / .875 for λcell=0\lambda_{\text{cell}} = 0 / .25 / .5 / 1 / 2, so the intermediate weights fall below the no-cell-term model while the default and twice-default exceed it, which is the pattern one expects when run-to-run variance is substantial. With only 15 and 8 healthy samples in the two external cohorts, as the authors note, a single healthy error moves balanced accuracy by .033 and .063. The cell-level effect is large enough to survive this uncertainty, but the sample-level conclusions that the abstract leads with are not established at a level I would consider robust. The path from token-level bias to sample-level transfer is asserted rather than demonstrated, and simpler alternatives are not ruled out. The sample-level gain appears only in the presence of sample-SIGReg: cell-SIGReg alone lowers external severity balanced accuracy from .459 to .422 and moves source-fitted AUROC by about +.01 on Geanon and +.005 on Penttilä. At the embedding level the paper reports that 10-nearest-neighbour label purity on the sample embeddings is the same for every model on both external cohorts (all between .39 and .48), and that cohort identity stays linearly decodable from every representation; so the mechanism by which a shared cell frame improves a source-fitted rule on the pooled embedding is left open, and the "associated with" hedge in the abstract is doing real work. The "no sample labels" framing is also somewhat overstated: sample membership within a mini-batch is available for free, so a direct penalty on the between-sample share of pooled-token variance, or a VICReg- or whitening-style penalty on pooled tokens, would be equally label-free and equally cheap. Neither is compared, and no label-free target-side normalization baseline is reported either. It therefore remains unclear whether the SIGReg statistic specifically, or any constraint on pooled token geometry, is what produces the gain, or whether part of it could be recovered by simple test-time normalization applied to a much simpler encoder.

Questions for authors
  1. Since each model is pretrained once, could you repeat the 2×2 conditions with additional pretraining seeds and report severity balanced accuracy, source-fitted AUROC and the interaction term with intervals over those seeds, together with paired intervals over external donors rather than over source splits only? The cell-weight sweep already varies at the sample level, so this is the analysis most likely to change my assessment of the sample-level claims.
  2. How does cell-SIGReg compare against simpler label-free constraints on the same pooled tokens at a matched weight, for example a direct penalty on the between-sample share of pooled-token variance using the within-batch sample index, or a VICReg- or whitening-style penalty? Since sample membership in a mini-batch is free, the absence of this comparison leaves open whether the SIGReg statistic specifically, or any constraint on pooled-token geometry, produces the gain. In the same spirit, would label-free target-side normalization, such as per-cohort marker standardization or per-sample token centering before pooling, close part of the Table 2 gap when applied to a reconstruction-only or MAESTRO encoder? The centering analysis in the appendix suggests this baseline is informative.
  3. What measurable property of zz accounts for the difference in source-fitted transfer? On the external cohorts, embedding-level label purity is indistinguishable across models, and cohort identity remains linearly decodable from every representation, so can you instead report how zz itself moves when disjoint cell subsets of the same donor are encoded, in units of between-donor spread, with and without cell-SIGReg?
  4. MAESTRO is retrained in its released-code configuration rather than its published one, with five encoder blocks and a 256-d embedding instead of three blocks and 1,024 dimensions. Does the comparison hold under the published configuration?
4 comments

Thank you for the review; the analyses you asked for in Q1 are now in the paper.

Weakness paragraph (single run, severity margin, interaction), Q1 → Blocks G1, G2 and G3. In brief:

  • Single run: Tables 1–3 now report three pretraining seeds, with donor-level bootstrap intervals per seed.
  • Severity margin: we agree that the margin was within the uncertainty of a 92-sample task with 14 samples in its smallest class. The revision drops severity grading and probes instead three clinical labels of a breast-tumour mass cytometry dataset that differs in institution, specimen type and marker panel (Table 1, Appendix J). SIGCell has the highest mean on all three tasks; a patient-level bootstrap separates it from MAESTRO on tumour versus juxta-tumoural tissue; on grade and nodal status the intervals include zero.
  • Interaction: the +.141 printed in the submission was one seed on the severity task. Over three seeds and on source-fitted transfer, the interaction is +.080 AUROC [+.020, +.160] and +.059 balanced accuracy [.000, +.117]. SIGCell matches cell-SIGReg alone in transferred balanced accuracy and is higher in AUROC (+.035 [+.002, +.076]; Appendix Table 21).

Cell-weight sweep

  1. The non-monotone sample-level rows of the sweep come from one pretraining seed, and we no longer read them as a dose response. The two ends of the sweep, which exist at three seeds, give a consistent sign.

  2. The sweep and the seed-by-seed comparison:

  • At seed 206, source-fitted balanced accuracy is .795, .695, .749, .918 and .889 for λ_cell = 0, .25, .5, 1 and 2.
  • The default alone spans .829–.918 across three pretraining seeds.
  • Seed by seed, the default is above the model without the cell term at every seed: +.123, +.128 and +.079 balanced accuracy, and +.092, +.108 and +.115 AUROC.
  • For the sample weight, the default keeps the higher source-fitted AUROC than λ_sample = 0 at all three seeds, with balanced accuracy within .02 at the other two.
  1. Section 5.5 and Tables 12–13 say so; the token-geometry rows, which change monotonically, are unchanged.

  2. The intermediate sweep points remain at one pretraining seed.

Path from token-level bias to sample-level transfer → Block G6.

"No sample labels": we agree; sample membership within a mini-batch is free, and an explicit penalty that uses it is in Block G4. The revision replaces "without sample labels" by "without using sample membership".

Q2, first part (simpler constraints) → Block G4.

Q2, second part (target-side normalization)

  1. Label-free target-side normalization does not close the gap; in almost every model and seed it lowers source-fitted transfer.

  2. Source-fitted AUROC, base → per-cohort marker standardization / per-sample token centering before pooling, three pretraining seeds, Table 2 protocol:

modelseed 206seed 207seed 208
SIGCell.968 → .808 / .886.951 → .827 / .910.914 → .878 / .901
MAESTRO.786 → .578 / .427.814 → .655 / .747.910 → .721 / .441
reconstruction only.879 → .694 / .509.897 → .737 / .713.925 → .708 / .585
  1. New Appendix Table 11.

  2. The base values come from a re-embedding of the external samples for this analysis and differ from Table 2 by up to .05.

Q3

  1. z is stable to which cells of a sample are encoded, in every model, so the requested measurement does not account for the difference. The context does: when the cells stay and the cells they are encoded with change, .53–.68 of the between-donor spread of z remains with cell-SIGReg and .23–.32 without it. Along the frozen source rule, the external class separation of the two groups of models differs by the part that a sample's own cells give.

  2. All measurements use real cells and the 15 models (five training conditions, three pretraining seeds). D is the between-donor spread of z on the source set.

  • Which cells (requested). Two disjoint 10,000-cell subsets of one sample move z by .010–.014 D without the cell term and .020–.022 D with it at the source, and by .028–.040 and .043–.049 on the external COVID-19 dataset. Across subset draws the source-fitted AUROC varies with an SD of at most .004.
  • Which context. We keep 5,000 cells of a sample fixed, encode them in chunks of 1,000 together with 9,000 cells of healthy donors of the source institution (the same cells for every sample), and pool z from the fixed cells only. The between-donor spread that remains is .53–.68 D with the term (SIGCell, cell-SIGReg only) and .23–.32 D without it (reconstruction only, sample-SIGReg only, MAESTRO). Three experiments with independently drawn cells, different donors in the context and four or sixteen donors per context give .51–.69 and .20–.35.
  • Along the source rule. The score of each sample splits exactly into what its cells give in the common context and what its own context adds. On the external COVID-19 dataset the class separation, in units of the source class gap, is .54–.72 with the term and .36–.53 without. The cells' part is .16–.35 against −.01–.09; the context's part is similar in the two groups (.23–.52 and .32–.47). Of the difference in separation, +.16, the cells give +.21 and the context −.04. The split was fixed before the data of the third experiment were read.
  • In AUROC. The context's part alone transfers at .83 with the term and .86 without (source-fitted AUROC, means over models). Adding the cells' part raises this by .11 with the term (.03 to .16 per model) and by .01 without (−.03 to .04).
  • A context that carries only the institution. We repeat the reading with the context taken from healthy donors of each sample's own institution, so that the context differs between institutions and says nothing about the sample. In that reading .69–.80 of the token variance of an encoder without the term lies between institutions, against .06–.08 with the term: without the term, the tokens of the same cells follow the context. The source-fitted AUROC of the frozen rule is .91 with the term and .62 without (means over models; +.25 and +.31 for the two sets of context donors), against .93 and .87 in the samples' own context.
  1. The revision reports these measurements in Section 5.4 and in a new Appendix L with a per-model table (Table 22), and Appendix M names the share of z written by a sample's own cells as the measurable property.

  2. Scope:

  • With five training conditions the property separates the two groups of models; it is a between-group property rather than a ranking within a group. In AUROC the accounting holds for the condition means, not model by model (one model with the term gains .03 from its cells, as much as the largest gain without it).
  • The term reduces the dependence of z on the context, and the context still contributes. Replacing the context moves z by .57–.66 D with the term (.70–.82 D without), the source-fitted AUROC of the models with the term falls from .93 to .78 in the common context, and within each of these models the cells give .28–.61 of its own external separation.
  • The cells' part is a share of the score. Read alone, it ranks the external donors equally well in the two groups (source-fitted AUROC .78 and .78); without the term it is small (its within-class spread is .10–.34 of that of the whole score, against .55–1.16 with the term), so it adds little to the whole.
  • The ranges of the external separation are close (.537 with the term, .534 without) and overlap under other heads; the two quantities that stay separated are the retained spread and the cells' part.
  • One set of four context donors can move a model's AUROC by up to .46, which is why each context is averaged over two sets. In the reading with the institution's context the two ranges touch (.83–.96 with the term, .49–.83 without), and in the common context the difference between the groups is −.00 with one set of donors and +.10 with the other.
  • The split is defined against a reference context of healthy source donors.

Q4

  1. The configuration we used is a published one: that of the MAESTRO authors' 2026 manuscript (Lee et al., bioRxiv 2026, doi:10.64898/2026.07.15.724605), which the released code implements. Its Methods (Sec. 3.3) specify:
  • five induced-point attention blocks with 16 learned points each, one attention head;
  • hidden size 384 and a 256-d latent;
  • EMA momentum 0.99, batch size 3 and 500 epochs.

Our MAESTRO run has each of these values.

  1. The ICLR 2025 paper describes an earlier configuration (three ISABs with 2,500 inducing points, a 1,024-d latent). The 2026 manuscript reports all of its results with the newer one.

  2. We have not run the ICLR 2025 configuration, so the comparison is established for the 2026 configuration only; Appendix N states both configurations.

Thank you for the thorough rebuttal. The three pretraining seeds with donor-level paired intervals, the three-seed interaction, the comparison with simpler pooled-token constraints, and the revised wording address most of my concerns, and the cell-level effect, which holds at every seed, is the robust core of the paper. Some points remain open: the sample-level comparisons for the alternative constraints and for MAESTRO + cell-SIGReg rest on single runs, the external benchmark was changed during the rebuttal, and the link from token geometry to sample-level transfer is still only associative, so I would keep the "associated with" hedge. I therefore keep my rating of 3.

Reviewer_zyiGOpenReview ↗
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Paper summary

This paper proposes SIGCell, a transferable set encoder for cytometry data. It identifies sample-context bias in masked set encoders, where cell representations depend heavily on their surrounding sample. To address this, the authors introduce cell-SIGReg, applying isotropic Gaussian regularization to cell tokens pooled across samples. Experiments on external cytometry datasets show improved cross-institution transfer, supported by ablations and representation analyses.

Critical strengths

The paper identifies a concrete limitation of existing set encoders. The sample-context bias analysis, particularly the context-swap experiments, provides useful evidence for this problem.

The proposed regularization is simple and achieves promising cross-institution transfer results. The controlled ablations help explain the contributions of cell-level and sample-level regularization.

Critical weaknesses

The external evaluation relies on two small datasets containing only 92 and 124 samples.

All datasets use the same 30-marker panel and focus mainly on COVID-19-related transfer tasks. Generalizability to other diseases, institutions, and marker configurations remains unclear.

The methodological novelty primarily comes from applying the existing SIGReg objective to cell-level representations. Comparisons with alternative token-level regularization or normalization methods are insufficient to establish the necessity of this design.

Proposition 1 characterizes the projected representation rather than the original cell-token space. The theoretical connection between the proposed regularizer, reduced sample-context bias, and improved transfer performance requires further clarification.

The claim that sample-context bias is a general failure mode of masked set encoders is supported by a relatively limited set of architectures and objectives.

Questions for authors

Clarify the theoretical connection between projected and original cell representations.

Provide stronger evidence for the stability and generalizability of external transfer results.

Clarify the advantages over simpler token-level regularization methods.

Discuss the generality of sample-context bias across set encoders.

A convincing resolution of these concerns would make me consider raising my rating to 3.

4 comments

Thank you for the review; each concern is answered below. Weakness 3 (second part) and Question 3 are answered in Block G4, Weakness 4 (second part) in Block G6, and Weakness 5 and Question 4 in Block G5.

Weakness 1, Question 2 (small external cohorts, stability)

  1. We evaluate source-fitted transfer on one external COVID-19 dataset instead of two small cohorts, and add donor-level uncertainty.

  2. The external COVID-19 dataset and the results:

  • The set combines Geanon, Penttilä and the healthy controls of a public amyotrophic lateral sclerosis (ALS) mass cytometry cohort: 225 samples, 115 donors, 32 healthy, at three institutions. One source rule and one threshold must serve all three institutions.
  • On this set, SIGCell's frozen linear probe reaches AUROC .959 and balanced accuracy .878 (mean over three pretraining seeds; .947–.975 and .829–.918 across seeds), first among the ten models.
  • At pretraining seed 206, a donor-level paired bootstrap separates it from every other row in balanced accuracy, and from every row except CellCnn in AUROC (+.032 [+.003, +.072], permutation p = .06). Block G2 and Appendix Table 20 give all three seeds.
  1. Section 4 defines the external COVID-19 dataset; Table 2 reports it; Appendix Table 20 gives the per-seed intervals.

  2. The external COVID-19 dataset still has 32 healthy samples, so one healthy sample is .016 of balanced accuracy.

Weakness 2 (other diseases, institutions and marker configurations)

We agree that all results in the submission come from one blood panel and from COVID-19 tasks. To test whether the method carries over, we re-ran the whole frozen linear-probing protocol on a dataset that differs on all three axes the reviewer names:

  • Institution: the breast-cancer mass cytometry atlas of Wagner et al. (Cell 2019, University of Zurich), unrelated to the cohorts in the paper.
  • Disease and specimen type: breast cancer, using dissociated tumour and juxta-tumoural tissue instead of blood.
  • Marker panel: their 36-protein tumour panel (epithelial, mesenchymal, signalling and a few immune markers). Only three of these markers (CD3, CD45, HLA-DR) are in our 30-marker panel.

The data are 217 samples from 163 patients (161 tumour, 51 juxta-tumoural, 5 reduction mammoplasty), with a median of 52,869 cells per sample and 13.4 million cells in total.

Protocol. We kept the Table 1 protocol unchanged:

  • Training: SIGCell and MAESTRO were pretrained from scratch on these 217 samples without labels, with the paper's settings: seed 206, 500 epochs, effective batch 12, 10,000-cell contexts, and the best-epoch checkpoint.
  • Training-free baselines: CKME, k-means and FlowSOM were fitted on the same samples.
  • One change: 19 samples have fewer than 10,000 cells, so cells were drawn without replacement and each batch was cut to the size of its smallest sample.
  • Evaluation: sample embeddings were frozen. We then ran five-fold cross-validation grouped by patient over ten split seeds, with a standard scaler and a class-balanced logistic regression (C = 1).
  • Tasks: we used the three clinical labels in the atlas: tumour versus juxta-tumoural tissue, histological grade (G1–2 against G3), and lymph-node status (N0 against N+, with N1mic counted as positive).

Results (balanced accuracy / AUROC, mean ± SD over ten split seeds):

taskn (patients)SIGCellMAESTROCKMEk-meansFlowSOM
tumour vs juxta-tumoural212 (160).926 ± .009 / .968 ± .006.897 ± .012 / .955 ± .004.897 ± .012 / .954 ± .007.897 ± .013 / .954 ± .005.884 ± .015 / .923 ± .006
grade G1–2 vs G3158 (152).735 ± .016 / .813 ± .020.717 ± .017 / .783 ± .016.717 ± .024 / .788 ± .021.654 ± .039 / .718 ± .047.656 ± .020 / .701 ± .017
node N0 vs N+153 (147).595 ± .032 / .638 ± .024.555 ± .034 / .596 ± .021.586 ± .048 / .609 ± .035.540 ± .023 / .571 ± .024.557 ± .028 / .572 ± .030

On this new institution, disease, specimen type and panel, SIGCell has the highest mean on all three tasks and both metrics.

For the uncertainty over patients, we ran a patient-level paired bootstrap: 2,000 draws of patients with replacement, the same draws for every model. Intervals are 95% percentile intervals for SIGCell minus each row, conditional on the pretrained checkpoints.

  • Tumour versus juxta-tumoural tissue: the interval excludes 0 against MAESTRO (BA +.030 [+.004, +.060], AUROC +.013 [+.001, +.027]) and against FlowSOM. It excludes 0 against CKME in BA only (+.030 [+.001, +.065]). Against k-means it does not exclude 0.
  • Grade: the interval excludes 0 against k-means (AUROC +.095 [+.011, +.176]) and FlowSOM (+.112 [+.023, +.210]). It includes 0 against MAESTRO (+.030 [−.015, +.074]) and CKME (+.025 [−.036, +.088]). SIGCell has the highest grade AUROC in 73% of draws.
  • Nodal status: every interval includes 0, and nodal status is hard for every model (AUROC at most .64).

SIGCell is first on all three tasks. With 153–212 samples the bootstrap separates it from the strongest baselines on tumour versus juxta-tumoural tissue, and on the two harder tasks it keeps the highest mean with intervals that include zero.

Scope.

  • It shows that the method trains without changes on a different specimen type and panel (tissue instead of blood, a non-immune panel) and gives the best frozen sample representation among the models we compared.
  • It is one additional dataset, with one pretraining run (seed 206) per model. Pretraining and probing use the same samples (labels are never seen during pretraining), as in the paper's Table 1.
  • SIGCell, like MAESTRO and the other set encoders, is pretrained per panel; transfer of one pretrained model across panels is a future direction.

The revision reports this experiment in Table 1 (replacing the severity task) and Appendix J, and Section 6 states the per-panel pretraining. See also Block G7.

Weakness 3, first part (what is new beyond the SIGReg statistic)

  1. The statistic is LeJEPA's, as the paper states. The paper adds the diagnosis of the sample-context bias and a different use of the statistic. In LeJEPA it guards one embedding against collapse; here it constrains the cell tokens pooled across samples, so that cells from different samples share one coordinate frame.

  2. With the same statistic, standardizing each sample on its own leaves the between-sample share at 1.00 after 100 epochs (one run). Pooling tokens across samples after a common standardization brings it to .095–.273 at 500 epochs (three seeds). Proposition 1 gives the second-moment reason.

  3. Contribution 2 is restated in these terms.

  4. Other constraints on the pooled tokens also restore the cell-type read-out, and cell-SIGReg transfers best at the sample level (Block G4).

Weakness 4, first part, Question 1 (Proposition 1 and the token space)

  1. We agree that Proposition 1 is a statement about the 64 coordinates the statistic tests. The revision now states exactly what follows from it for the 384-d tokens, and reports, for three pretraining seeds, what each part of the token space carries. The head plays the role that the projector plays in self-supervised learning: the constraint is imposed on its output, and the representation that is read is the layer before it (Bordes et al., Guillotine Regularization, TMLR 2023).

  2. What is exact (new Corollary in Appendix B):

  • The tokens split into the head directions (the 64-dimensional row space of the head's linear map) and their complement (the other 320 directions). The between-sample share of the tokens is the variance-weighted mean of the shares of the two parts, share = ρ · share_head + (1 − ρ) · share_comp, where ρ is the fraction of token variance in the head directions. Proposition 1 constrains the first term only (the tested cloud depends on the tokens through the head directions alone) and leaves the second free.
  • The proposition is a rank argument, and the same argument holds in any space: in a batch of S samples the between-sample share of a representation is at most the fraction of its batch variance in its top S − 1 principal directions. Proposition 1 is the isotropic case.
  • A cap on the between-sample share is also a cap on every coarser grouping of the samples (batch, study, institution), because the variance between group means cannot exceed the variance between sample means.

What is measured (five training conditions, three pretraining seeds each; ranges over seeds and conditions):

  • Head directions. They hold .09–.10 of the token variance. Their between-sample share is .040–.052 at the source and .059–.086 on the external COVID-19 dataset, below the raw markers (.19 and .15). Their between-institution share is .005–.011, against .08 for the raw markers.
  • Complement. Its between-sample share is .25–.36 with cell-SIGReg, against .96–.99 for the tokens of the encoders without it (which have no head), and its between-institution share .04–.06 against .13–.17 (raw markers .08). In batches of twelve samples the spectral cap on the tokens is .40–.46 with the term (measured share .22–.32) and .97–.99 without (.96–.99).
  • Which part is read. The head directions hold .02–.03 of the between-sample variation of the pooled token from which z is computed, where 64 random directions would hold .17. The sample means of the head coordinates separate COVID-19 from healthy source samples with a cross-validated AUROC of .57–.70, against .95–.98 for z. A linear read-out of 14 cell types from the head directions reaches balanced accuracy .16–.23 on the external COVID-19 cohorts (chance .07), against .62–.70 from the tokens and from the complement.
  • What remains between samples. Without the term, .97–.99 of a sample's imprint on its tokens is one offset common to all its cell types. With the term this fraction is .72–.77 on the external samples, the level of the raw markers (.78).
  1. The caveat that closed Section 3.2 is now part of the statement of the proposition, and Section 3.2 says that the head is a projector. The proof moves to Appendix B, which adds the corollary (Corollary 1) and a table of what the head directions and their complement carry in the 15 models (Table 5).

  2. The effect on the complement goes beyond what the proposition guarantees, so we measure it: the gradient of the term reaches the tokens only inside the 64 head directions, and the complement changes because the two parts are produced by the same encoder. Its between-sample share falls from .96–.99 without the term to .25–.36 with it, at every seed.

Thank you for the donor-level analysis, the new breast cancer results, and the clarification of Proposition 1. These address the concerns I raised in my review. Taking the other reviewers’ comments into account as well, I’ve decided to keep my original rating.

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Paper summary

This paper studies cross institution transfer of pretrained CyTOF set encoders under a fixed 30 marker panel, with particular emphasis on whether a frozen representation remains useful without target cohort labels. Despite using the same commercial panel, the three cohorts exhibit substantial institution specific shifts: cohort identity is perfectly decodable from raw marker intensities and gated cell composition, and the shift persists among healthy donors and within individual gated cell types.

The paper identifies a sample context bias in masked set encoders. Because each cell token is computed jointly with other cells from the same sample while reconstruction supervises only the pooled sample embedding, the same cell can receive substantially different token coordinates under different sample contexts. Without cell level regularization, 0.93 to 0.98 of token variance lies between samples, compared with 0.10 to 0.19 for raw markers, and changing only the surrounding sample moves the same cells by roughly 6 to 9 times their intrinsic cell to cell spread. SIGCell addresses this problem by applying SIGReg not only to the sample embedding but also to projected cell tokens pooled across samples. Proposition 1 shows that, after groupwise standardization, an isotropic cell cloud can place at most (S−G)/d(S-G)/d of its variance between samples, which equals 8/64=0.1258/64=0.125 under the training layout.

Empirically, SIGCell retains competitive internal performance while improving transfer. On the internal 13 class task it reaches 0.789 balanced accuracy versus 0.791 for MAESTRO, while on external four class COVID 19 severity grading it reaches 0.501 versus 0.439 for MAESTRO and 0.441 for CKME. In source fitted COVID 19 detection, its frozen encoder with only a linear probe achieves AUROC 0.949 on Geanon and 0.995 on Penttilä, ranking first among the ten evaluated models. Controlled ablations further show that adding cell SIGReg to sample SIGReg raises the external cell type readout from 0.133 to 0.635 on Geanon and from 0.191 to 0.757 on Penttilä, while reducing the between sample variance share to 0.12 to 0.24 and the context swap displacement to about one cell spread. The two regularizers interact positively on external severity grading, with an interaction of +0.141+0.141.

Critical strengths

S1. The paper identifies and carefully characterizes sample-context bias as a reusable finding rather than a method-specific failure. Two aspects are particularly convincing. First, the bias already exists at random initialization, where .949, .971, and .956 of token variance lies between samples across the three cohorts. Figure 9 further clarifies that epoch 0 is the same random initialization shared across the training trajectories. The bias is then retained by reconstruction, sample-SIGReg, and MAESTRO self-distillation. For example, MAESTRO reaches between-sample shares of .98, .97, and .97 and a context-swap displacement of 7.5 cell spreads, compared with 6.4 under reconstruction alone. Second, the diagnosis is supported by complementary label-free controls. Re-encoding the same cells with other cells from their original sample changes their tokens by only 0.05 to 0.29 spreads, whereas changing the sample context produces much larger shifts. Without the cell term, the mean token displacement is also highly aligned with the shift of the new context cloud, with cosine similarity .98 to .99. GPCT provides an informative counterexample: although its cells are also jointly encoded, its between-sample share is only .22 to .32 and its context-swap displacement is about 0.8 spreads. Together, these results isolate sample context as the relevant source of distortion and show that joint encoding alone is insufficient to explain the effect.

S2. The controlled ablation provides unusually transparent evidence about where the gains come from, including results that are unfavorable to individual components. The four SIGCell conditions in Table 3 share the encoder, reconstruction pretext, corpus, training budget, and seed, differing only in latent-space regularization. Importantly, sample-SIGReg alone performs worse than reconstruction alone on every external readout, despite giving the strongest internal probe. The full configuration also sacrifices internal balanced accuracy relative to sample-SIGReg alone, .789 versus .807. The external benefit therefore cannot be explained as a simple additive gain from two independently useful regularizers. Appendix E instead shows positive interaction effects of +.141, +.109, and +.071 on the three external balanced-accuracy readouts, while the interaction is slightly negative internally. The cell term itself produces a large controlled effect on cross-sample cell-type transfer, raising balanced accuracy from .133 to .635 on Geanon and from .191 to .757 on Penttilä when sample-SIGReg is present. All Table 3 conditions without the cell term remain at or below .191 on Geanon. The weight sweep further shows a monotonic reduction in sample-context bias as λcell\lambda_{\mathrm{cell}} increases, with between-sample share falling from .98 to .15 and context-swap displacement from 8.9 to 0.9, while λcell=2\lambda_{\mathrm{cell}}=2 improves cell-type readouts but slightly reduces severity performance relative to the default. The paper also appropriately distinguishes this controlled evidence from Table 2, which explicitly compares whole models with different architectures, pretraining objectives, and sizes.

Critical weaknesses

W1. The external results that support the paper's headline claims are reported without uncertainty over the target cohorts, making several of the smaller performance margins difficult to interpret. In Table 2, SIGCell leads on all four source fitted transfer metrics, but some margins are narrow: on Penttilä, AUROC is .995 versus .989 for cyMAE and CellCnn; on Penttilä balanced accuracy it is .965 versus .935 for CytoDx; and on Geanon balanced accuracy it is .871 versus .861 for Set Transformer. The latter difference is also smaller than Set Transformer's reported seed variability of .023. More importantly, these standard deviations do not quantify uncertainty in the external cohorts. For the frozen rows, each seed repartitions only the 322 source samples, while the same fixed external cohort is evaluated every time. The appendix explicitly states that the resulting variation reflects sensitivity to which source samples were available. This distinction matters because the external cohorts are small. The paper itself notes that the Geanon severity task has only 92 samples with 14 in its smallest class, while the binary transfer evaluations contain only 15 healthy Geanon samples and 8 healthy Penttilä samples; consequently, one healthy classification error changes binary balanced accuracy by .033 and .063, respectively. I also find no reported confidence interval, bootstrap analysis, p value, or hypothesis test comparing SIGCell with any baseline. The paper therefore establishes point estimate superiority, but does not establish whether its smaller external margins are statistically resolvable on these target cohorts. A paired target level uncertainty analysis, preferably resampling donors to respect repeated samples, would substantially strengthen the central transfer claims.

W2. The experiments establish the effectiveness of cell-SIGReg within the proposed training family, but do not test the broader claim that it is a generally useful regularizer for cytometry set encoders. The controlled 2 by 2 ablation in Table 3 is strong evidence that adding the cell term improves this backbone under the proposed reconstruction setup, because encoder, pretext, corpus, budget, and seed are held fixed. However, cell-SIGReg is never added to an independently defined pretrained encoder. This distinction matters because the abstract concludes more generally that cell level latent regularization improves cross institution transfer in cytometry set encoders. MAESTRO would provide a particularly informative test: the paper already retrains it on the same corpus and budget, uses a closely matched five ISAB, width 384 backbone, and shows that its cell tokens exhibit severe sample context bias. Yet MAESTRO is evaluated only with its original self-distillation objective, not with cell-SIGReg added to that objective. The authors themselves correctly caution that Table 2 compares whole models whose architecture, pretraining, and size differ, so that table cannot establish portability of the regularizer. A second experiment would also clarify whether training time regularization is necessary. Table 7 shows that simply subtracting each sample's mean token, a label free inference time operation, recovers a substantial fraction of the lost cross sample cell type readout without cell-SIGReg. For example, the Geanon readout rises from .133 to .397 at λcell=0\lambda_{\mathrm{cell}}=0, while reconstruction only rises from .164 to .426. However, the centered evaluation is reported only for the authors' ablation family, not for MAESTRO or other contextual encoders. Applying cell-SIGReg to at least one independent encoder, and applying the centering diagnostic to MAESTRO, would separate a generally useful regularization principle from an effect specific to the proposed training configuration.

W3. The cell type transfer diagnostic would be substantially easier to interpret if the raw markers were included as a reference on the external cohorts. Table 6 shows that, internally, a linear readout on the 30 raw markers reaches .97 balanced accuracy across samples, compared with .77 for SIGCell and .54 for MAESTRO. Yet the corresponding raw marker readout is not reported for Geanon or Penttilä, precisely where the paper emphasizes the large improvement from approximately .13 to .19 without the cell term to .64 to .69 with it. The appendix even notes that a pointwise representation has no sample context bias and therefore transfers cell type readouts naturally. Reporting the same source fitted raw marker classifier on all three cohorts would clarify whether cell-SIGReg restores transferable cell identity information toward the measurement level, or merely improves substantially over strongly distorted contextual representations.

W4. The paper does not quantify the training time or memory overhead introduced by cell-SIGReg. Appendix B makes clear that the additional statistic is nontrivial: the cell site processes up to 24,576 projected tokens through 512 random directions and 17 integration knots, with cost linear in the number of tokens. Table 13 reports fitting times for supervised baselines and identifies the four A100 GPUs used for pretraining, but it also states that the SIGCell run of record retained no timing log. A simple wall clock or step time comparison between reconstruction only and SIGCell would make the practical cost of the regularizer clear.

Questions for authors
  1. Could you provide paired uncertainty for the main external comparisons? For Table 1, since all models use identical donor grouped folds, please report the seed wise paired difference between SIGCell and the strongest competing representations, together with the SD of that difference, as is already done for the ablations in Figure 11. For Table 2, the reported SD for frozen encoders reflects variation in the source folds rather than uncertainty in the fixed external cohort. Could you additionally report donor level bootstrap confidence intervals, or an equivalent paired donor level analysis, for the performance difference between SIGCell and the closest competitors on Geanon and Penttilä? This seems particularly important for comparisons such as .995 versus .989 AUROC on Penttilä. If these rankings are not statistically distinguishable at the available cohort sizes, stating that explicitly would make the conclusions easier to assess.
  2. Does cell SIGReg provide the same benefit when added to another contextual set encoder? MAESTRO is already retrained on the same corpus and training budget and uses a closely matched encoder architecture. Could you add the cell SIGReg term to MAESTRO's original training objective and report the resulting between sample variance share, context swap displacement, cell type transfer readout, and external sample level performance? This experiment would directly test whether the benefit of cell level latent regularization transfers beyond the SIGCell objective family.
  3. What is the raw marker reference for the external cell type transfer readout? Table 6 reports .97 balanced accuracy from the raw 30 markers on the internal cell type readout, compared with .77 for SIGCell. Could you report the corresponding raw marker results on Geanon and Penttilä under exactly the same source fitted protocol? Since the paper describes pointwise representations as transferring cell type readouts naturally, including this reference would clarify whether cell SIGReg restores information lost by contextual encoding and how close the learned representation comes to the measurement level reference.
  4. How much of the observed sample context failure can be corrected at inference time by centering other contextual encoders? Table 7 shows that subtracting each sample's own mean token substantially recovers cross sample cell type transfer without the cell term, but this analysis is restricted to the SIGCell ablation family. Could you apply the same label free centering operation to MAESTRO and GPCT and report their external cell type readouts before and after centering? This would clarify how much of the benefit of training time cell regularization can be reproduced by a simple inference time correction.
  5. Could you make the cell type readout protocol fully self contained? Please specify the classifier used for the cell level readout, how the donor grouped internal source subset is constructed for each seed, and how many cells per cell type and cohort are sampled. Table 7 states that the classifier and source split follow Table 8, while Table 8 primarily reports the resulting metrics and sensitivity sweep. Since this readout supports the paper's largest controlled effect, its complete fitting and sampling procedure should be recoverable from a single protocol description.
  6. What is the computational overhead of cell SIGReg, and will the exact pretrained checkpoints used for the reported results be released? The cell statistic evaluates up to 24,576 projected tokens through 512 directions and 17 integration knots at each training step. Could you report the wall clock step time, total pretraining time, or percentage slowdown relative to reconstruction without the cell term? In addition, the paper provides an anonymous code repository and states that the pretrained comparison models were retrained on the common corpus and panel. Will the exact SIGCell and retrained baseline checkpoints used for the reported tables also be released? Providing these checkpoints would substantially improve exact reproducibility of the cross model results.
2 comments

Thank you for the review; the weaknesses and questions are answered in order.

W1, Q1

  1. We now report the seed-wise paired difference between SIGCell and every other row of Table 2 with its SD, and donor-level bootstrap intervals for each seed (Block G2; new Appendix Table 20).

  2. Source-fitted transfer, SIGCell minus each row:

  • Entries are the difference at each seed; the last column is the mean ± SD over seeds.
  • Pretraining seeds 206 / 207 / 208; MAESTRO is paired seed by seed.
  • ✔ marks an interval that excludes zero together with permutation p < .05.
AUROC s206s207s208mean ± SDBA s206s207s208mean ± SD
MAESTRO+.170 ✔+.156 ✔+.040 [.000, .083]+.122 ± .071+.201 ✔+.175 ✔+.014 [−.046, .074]+.130 ± .101
cyMAE+.073 ✔+.053 ✔+.045 ✔+.057 ± .014+.111 ✔+.079 ✔+.022+.071 ± .045
Set Transformer+.067 ✔+.047+.040+.051 ± .014+.076 ✔+.044−.012+.036 ± .045
CellCnn+.032+.011+.004+.016 ± .014+.208 ✔+.176 ✔+.120 ✔+.168 ± .045
GPCT+.057 ✔+.037+.029+.041 ± .014+.234 ✔+.202 ✔+.145 ✔+.194 ± .045

(The full table with all nine rows and intervals is Appendix Table 20.)

Frozen linear probing (Table 1):

  • Blood pretraining eleven-diagnosis balanced accuracy, SIGCell minus MAESTRO paired seed by seed: −.004, −.006 and −.004. The donor intervals include zero at every seed.
  • Against CKME, the same difference is +.059, +.051 and +.051, and the interval excludes zero at every seed.
  • On the new breast-tumour tasks (one pretraining run), a patient-level bootstrap separates SIGCell from MAESTRO on tumour versus juxta-tumoural tissue (BA +.030 [+.004, +.060], AUROC +.013 [+.001, +.027]); on grade and nodal status it keeps the highest mean with intervals that include zero (Appendix Table 19).
  1. Direct answer to the last sentence of Q1: at these cohort sizes, the intervals of the following differences include zero, and Sections 5.1 and 5.2 now say so:
  • the blood pretraining difference to MAESTRO;
  • the breast-tumour grade and node differences;
  • the seed-208 difference to MAESTRO;
  • the AUROC differences to CellCnn, Deep Sets and GPCT at two seeds (against Set Transformer the intervals exclude zero at every seed, with permutation p ≥ .05 at two).
  1. The intervals reflect target-donor sampling only, with the fits held fixed. One healthy sample is .016 of source-fitted balanced accuracy.

W2 (independent encoder), Q2 → Block G5.

W2 (scope of the abstract) The abstract now reads "masked set encoders" in both places; the conclusion rests on the two encoders the term was added to (Block G5).

W2 (centering), Q4

  1. We report the requested numbers:
  • Subtracting each sample's mean token raises MAESTRO's cell-type read-out from .191 to .639 on Geanon and from .573 to .830 on Penttilä (.535 → .851 on the blood pretraining dataset).
  • GPCT, whose read-out is already near the raw markers, is unchanged (.846 → .849 and .879 → .877).
  • SIGCell reads .635 / .757 across samples and .684 / .765 after centering.
  1. These use the same cells, classifier and ten split seeds as Table 9 (SD .005–.029 over split seeds). Table 9 gains MAESTRO, GPCT and raw-marker columns.

  2. A higher cell-type read-out after centering does not make the sample representation transferable.

  • Centering acts on the tokens. When the same centered tokens are pooled into the sample embedding, the source-fitted rule of Table 2 transfers worse on the external COVID-19 dataset.
  • MAESTRO: AUROC falls from .786 to .427 (balanced accuracy .701 → .518). Reconstruction only: from .879 to .509 (.806 → .551). Both are pretraining seed 206, mean over ten split seeds; the same fall appears at the other two seeds.
  • The sample mean that centering removes is part of what the sample embedding needs.
  1. The training-time term does not have this cost. Added to MAESTRO's own objective (Block G5; same corpus, seed 206 and 500 epochs), cell-SIGReg does two things together:
  • It raises the cell-type read-out to .599 / .793 (.816 on the blood pretraining dataset).
  • It improves the source-fitted transfer of the same encoder: AUROC .804 → .889, balanced accuracy .717 → .819.
  1. Each model is one pretraining run, and the ± are over split seeds.

W3, Q3

  1. Under the same source-fitted protocol, a classifier fitted on the 30 raw markers of the source cells reaches .970 on the blood pretraining dataset, .857 on Geanon and .888 on Penttilä. Against this reference, a masked set encoder without the cell term loses most of the cell-type information that transfers across samples, and cell-SIGReg recovers it monotonically as its weight grows.

  2. The table gives balanced accuracy over fourteen cell types. The classifier is fitted on the source half of the blood pretraining dataset and applied unchanged; values are means over ten split seeds (SD ≤ .026; ≤ .003 for the raw markers).

λ_cell (λ_sample = .05)0.25.51 (SIGCell)2raw markers
blood pretraining.176.618.726.770.826.970
Geanon.133.510.601.635.721.857
Penttilä.191.643.732.757.801.888
  • Gap recovered: measured from the encoder without the cell term to the raw markers, the default weight recovers 75%, 69% and 81% of the gap (blood pretraining, Geanon, Penttilä), and twice the default weight recovers 82%, 81% and 88%.
  • Other encoders: cyMAE and CytoBERT, which encode each cell from its own markers alone, sit at the raw-marker level (.818 / .876 and .848 / .886 on Geanon / Penttilä), and so does GPCT (.851 / .882), whose cells attend to one another. The loss therefore belongs to masked set encoders trained without the cell term, and cell-SIGReg removes it there.
  1. A raw-marker row is added to Tables 3 and 9 and as a column of Table 12.

  2. Inside one sample, the tokens without the cell term still separate the cell types (.80 on the blood pretraining dataset, against .83 for the raw markers; Table 9). What these encoders lose is therefore the comparability of token coordinates across samples, and this read-out measures how much of it cell-SIGReg restores.

W4, Q6 (cost)

  1. The cell term adds little cost: the full SIGCell objective, reconstruction with both SIGReg terms, costs +10.7% per step over reconstruction alone, which bounds the cost of the cell term.

  2. We timed the paper's training layout: four A100-80GB GPUs × three samples, 10,000-cell contexts, step time taken from the slowest rank, 50 warm-up and 200 timed steps per round, three rounds per objective:

  • Median optimizer step: 1.48 s for reconstruction only and 1.64 s for SIGCell (both SIGReg terms; +10.7%), within the round-to-round variation.
  • Peak memory: 8.89 against 8.93 GB per GPU (+0.04 GB).
  • The cell term is computed on at most 2,048 visible-cell tokens per sample projected to 64 dimensions.
  1. The revision states both numbers in Appendix H.

  2. These are training-time measurements; inference is unchanged, because the projection head is not used to encode samples.

Q5 The revision gives the cell-type read-out protocol in one paragraph of Appendix H: classifier, construction of the donor-grouped source half per split seed, cells drawn per cell type and cohort, context size, and the number of scored cells (32,953 blood pretraining, 48,914 Geanon, 49,843 Penttilä at split seed 0).

Q6 (checkpoints) The whole-blood pretraining dataset is held under a data use agreement, and its data provider declined the release of model weights trained on it, citing participant privacy. We therefore cannot release the checkpoints during the review period; after publication, the SIGCell checkpoints will be available upon request. The full code, configurations and evaluation scripts are released, and all the other datasets are public.

Comments on the paper

3 comments

G1. Three pretraining seeds (XUfQ-Weakness1 / Weakness3 / Question1, a8QA-Weakness1, zyiG-Weakness1 / Question2)

  1. We now report SIGCell, MAESTRO and the four ablation conditions over three pretraining seeds each (same corpus, schedule and evaluation code), and Tables 1–3 of the revision print the three-seed mean ± SD. The cell-level effect of cell-SIGReg holds at every seed. At the sample level SIGCell remains first on source-fitted transfer in the three-seed mean, with the per-seed comparisons stated in Block G2.

  2. Each value is a mean over ten split seeds, so the spread across seeds is pretraining variation.

  • Source-fitted transfer (225 external samples):
    • SIGCell AUROC .975 / .954 / .947 and BA .918 / .886 / .829 (mean .959 / .878).
    • MAESTRO .804 / .798 / .907 and .717 / .711 / .815 (mean .837 / .748).
  • Blood pretraining eleven-diagnosis probe: SIGCell .770 ± .005 and MAESTRO .774 ± .004.
  • In the 2×2 ablation (Table 3), a bootstrap over pretraining seeds, split seeds and external donors gives:
    • the cell term's main effect on source-fitted AUROC: +.065 [+.030, +.099];
    • the interaction of the two terms: +.080 [+.020, +.160].
    • Against cell-SIGReg alone, SIGCell is higher in AUROC (+.035 [+.002, +.076]) and matches it in balanced accuracy (+.003 [−.043, +.045]).
  • Cell level:
    • Cell-type read-out on Geanon is .635 / .719 / .639 with both terms and .674–.691 with cell-SIGReg alone, against .111–.191 for every condition without the cell term.
    • Between-sample share of token variance is .095–.273 with the cell term and .913–.979 without it, on all three cohorts.
  1. The revision prints three-seed means in Tables 1–3, adds the seed-wise paired differences (new Appendix Table 20) and the bootstrap of the 2×2 effects (Table 21). "First among ten" in the abstract and conclusion now refers to the three-seed mean. The abstract, Section 5.4 and the conclusion also state the between-sample share over three seeds (.91–.98 without the cell term, .10–.27 with it). Because SIGCell and MAESTRO are now also pretrained on a breast-tumour dataset, the revision calls the submission's pretraining cohort the whole-blood pretraining dataset (blood pretraining dataset for short), and the three external cohorts used for source-fitted transfer together the external COVID-19 dataset.

  2. The bootstrap includes run-to-run variance as estimated from three pretraining runs per condition. The other pretrained comparison models (cyMAE, GPCT, CytoBERT) remain at one pretraining seed; the models that train a network on the source labels are averaged over ten training seeds.

G2. Uncertainty over target donors; seed-wise paired differences (a8QA-W1 / Q1, XUfQ-Q1 / W2, zyiG-Q2)

  1. The SDs in the tables describe source or evaluated-cohort splits. We now add donor-level paired bootstrap intervals and, as requested, the seed-wise paired difference between SIGCell and each other row of Table 2, with the SD of that difference.

  2. Design:

  • External donors are resampled with replacement within class and within cohort (Geanon 15 healthy / 43 COVID-19 donors, Penttilä 8 / 40, ALS healthy controls 9).
  • All samples of a donor stay together.
  • The source-fitted rules and their threshold are fixed.
  • Both models are scored on the same 2,000 resamples, and we report 95% percentile intervals per pretraining seed.
  • A difference is marked when the interval excludes zero and a donor-level paired permutation test gives p < .05 (uncorrected, descriptive).

Results:

  • Against MAESTRO, the paired difference is +.122 ± .071 AUROC and +.130 ± .101 balanced accuracy.
    • The interval excludes zero at two of three seeds.
    • It includes zero at the third (seed 208: +.040 [.000, .083] AUROC, +.014 [−.046, .074] BA), where MAESTRO has its strongest run and SIGCell its weakest.
  • In balanced accuracy, the interval excludes zero at all three seeds against CellCnn, Deep Sets, GPCT, CytoBERT, CytoSet and CytoDx.
  • In AUROC, SIGCell is above every row at every seed, and the interval excludes zero at all three seeds against cyMAE, CytoBERT, CytoSet and CytoDx. The difference is not marked against CellCnn at any seed, or against Deep Sets, GPCT and Set Transformer at two of three. These four models reach a high AUROC but a low balanced accuracy at the transferred threshold.
  1. New Appendix Table 20 gives every pair and seed; the captions of Tables 1–3 name the source of each ±; Section 5.2 states the per-seed outcome of these comparisons.

  2. The intervals condition on the fitted rules and reflect target-donor sampling only. One healthy sample is .016 of source-fitted balanced accuracy. Donor keys are derived from file names (patient identifiers are blank in both public cohorts).

G3. What the revised paper claims (a8QA-W2b, XUfQ-W1, zyiG-Q2)

(i) Masked set encoders trained only through the sample embedding carry a sample-context bias: the between-sample share of token variance is .913–.979 for three objectives at three seeds each.

(ii) Cell-SIGReg removes most of it (.095–.273) and lets a cell-type read-out fitted at the source transfer:

  • Geanon: .635–.719, against .111–.191 without the cell term.
  • Penttilä: .757–.819, against .184–.572 without it.
  • This holds at every seed.

(iii) As a frozen representation, SIGCell matches MAESTRO in distribution (.770 against .774 balanced accuracy; the donor interval of the difference includes zero at every seed). On the external COVID-19 dataset it is first in the three-seed mean among the ten models compared (AUROC .959, balanced accuracy .878). We state per seed where that ordering is and is not resolved (Block G2).

G4. Other label-free constraints on the pooled tokens (XUfQ-W7 / Q2a, zyiG-W3b / Q3)

  1. Four of five other label-free constraints on tokens pooled across samples also restore the cell-type read-out, which confirms the role of the pooled population. The fifth, a penalty on the between-sample share of the 64-d head alone, meets its own target on the head but leaves the token share at .67–.82 and the read-out at its level without the cell term. At the sample level, SIGCell's source-fitted transfer is higher than that of each of the five at the same seed, in AUROC and balanced accuracy, with donor-bootstrap intervals that exclude zero.

  2. Alternatives: one pretraining run each at seed 206, 500 epochs, same corpus and budget.

  • Cell-type read-out on Geanon / Penttilä (mean over ten split seeds):
    • the same SIGReg statistic on a 16-d head: .647 / .735;
    • a covariance-to-identity penalty on the pooled tokens: .681 / .784;
    • that covariance penalty on the 64-d head: .627 / .788;
    • an explicit between-sample-variance penalty that uses the within-batch sample index, combined with that covariance penalty: .697 / .759;
    • the between-sample share penalty on the 64-d head: .185 / .279;
    • SIGCell at the same seed: .635 / .757.
  • Source-fitted transfer, SIGCell minus each alternative at seed 206 (donor-bootstrap 95% interval, AUROC / balanced accuracy):
    • 16-d head: +.053 [+.021, +.095] / +.077 [+.036, +.129];
    • covariance penalty: +.069 [+.038, +.103] / +.102 [+.063, +.146];
    • covariance penalty on the 64-d head: +.029 [+.008, +.056] / +.043 [+.015, +.080];
    • covariance + between-sample penalty: +.039 [+.009, +.079] / +.083 [+.041, +.128];
    • share penalty: +.110 [+.052, +.181] / +.118 [+.063, +.179].
  1. New Appendix E (Table 10) lists every constraint with its layout, between-sample share, cell-type read-out and source-fitted transfer. Sections 1 and 3 no longer present the SIGReg statistic as necessary for the cell-level effect; contribution 2 is restated as the choice of population (tokens pooled across samples after a common standardization) and of statistic for transfer.

  2. The alternatives are one run each. A VICReg-style variance–covariance penalty belongs to the same family as our covariance row; we did not run that exact form or a whitening layer.

G5. Adding the term to an independently defined encoder (a8QA-W2a / Q2, zyiG-W5 / Q4)

  1. We added cell-SIGReg (weight 1) to MAESTRO's own objective and changed nothing else: same corpus, seed (206) and 500-epoch schedule. The token-level effect carries over, and source-fitted transfer improves with it.

  2. Token level (read-outs: mean ± SD over ten split seeds):

MAESTRO+ cell-SIGReg
Between-sample share, blood pretraining / Geanon / Penttilä.976 / .974 / .965.467 / .427 / .318
Context-swap displacement (cell spreads)7.461.24
Cell-type read-out, blood pretraining.535 ± .018.816 ± .016
Cell-type read-out, Geanon.191 ± .026.599 ± .022
Cell-type read-out, Penttilä.573 ± .016.793 ± .008
  1. Sample level (mean ± SD over ten split seeds):
MAESTRO+ cell-SIGReg
Source-fitted AUROC.804 ± .003.889 ± .004
Source-fitted balanced accuracy.717 ± .006.819 ± .007

The paired gain is +.085 AUROC and +.102 balanced accuracy. Against MAESTRO's three pretraining seeds (.798–.907 AUROC, .711–.815 balanced accuracy), MAESTRO with cell-SIGReg lies in the upper part of the AUROC range and above the whole balanced-accuracy range.

  1. Revision: Appendix Table 8 reports this comparison; contribution 1 is scoped to masked set encoders.

G6. From the regularizer to transfer: three links (zyiG-W4b, XUfQ-W5 / W9)

  1. We separate three links and state the evidence for each. For the third, from token geometry to sample-level transfer, the revision adds a measured property of z that accounts for the difference between the training conditions; we have no derivation of it.

  2. The three links:

  • From the objective to token geometry. Controlled training at three seeds moves the between-sample share from .913–.979 to .095–.273. At one seed it responds monotonically to the cell weight (share .98 → .15, context-swap displacement 8.9 → 0.9).
  • From token geometry to cell-type read-out transfer. At three seeds the read-out on Geanon moves from .111–.191 to .635–.719. Inside fixed checkpoints, subtracting each sample's mean token raises the read-out without the cell term, from .133 to .397 and from .164 to .426 on Geanon.
  • From token geometry to sample-level transfer.
    • Seed by seed, the cell term raises source-fitted AUROC by .092, .108 and .115 at the three seeds (Table 12). Over three seeds its main effect is +.065 [+.030, +.099].
    • Removing the sample mean from the tokens without training does not reproduce this. Per-sample token centering before pooling lowers source-fitted AUROC: MAESTRO .786 → .427, .814 → .747, .910 → .441; reconstruction only .879 → .509, .897 → .713, .925 → .585 (Table 2 protocol, three pretraining seeds).
    • The conditions are separated by the share of z written by a sample's own cells. Read in a common context (the same healthy source donors' cells for every sample), z keeps .53–.68 of its between-donor spread with the cell term and .23–.32 without. Along the frozen source rule, the external class separation of the two groups differs by +.16 source class gaps: +.21 from the part the cells give and −.04 from the part the context adds (15 models; Appendix L, Table 22; answer to XUfQ Q3).
  1. Section 5.4 and the new Appendix L report this measurement, and Appendix L states its scope.

  2. The property separates the models with and without the cell term; it is a between-group property rather than a ranking within a group. The cell term reduces the dependence of z on its context, and the context still contributes: read in the common context, source-fitted AUROC is .78 with and without the term (.93 and .87 in the samples' own context). That a constraint on the 64 tested coordinates changes the other 320 token directions is likewise an empirical finding (answer to zyiG Question 1).

G7. Scope (zyiG-W1 / W2, a8QA-W2b)

  1. The blood cohorts share one 30-marker panel and the external blood tasks concern COVID-19. To test beyond this, we added a breast-tumour dataset with a different 36-marker panel from another institution, pretrained without labels and probed on its own samples (see our response to Reviewer zyiG, Weakness 2).

  2. The external COVID-19 dataset is 225 samples from 115 donors at three institutions, 32 of them healthy; COVID-19 cases come from two of them, and the third contributes nine healthy controls.

  3. Section 6 states that SIGCell reads a fixed marker panel and is pretrained per panel, and that source-fitted transfer is tested for COVID-19 against healthy, the diagnosis for which public cohorts share the 30-marker panel; the last sentence of the abstract is scoped to masked set encoders.

  4. SIGCell, like the other set encoders, is pretrained per panel; transfer of one pretrained model across panels is the future direction as mentioned in Section 6.

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

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