acceptodds
Under review as a conference paper at ICLR 2027

HiLL: LLM-based Recursive Semantic Refinement for Reference-Free Cell Type Annotation

Abstract

Single-cell RNA sequencing and spatial transcriptomics provide high-resolution profiles of tissues, but translating these profiles into biological insights critically depends on accurate cell type annotation. Manual annotation is labor-intensive, difficult to scale, and dependent on expert knowledge, motivating automatic annotation methods. However, automatic cell type annotation often relies on external annotated atlases, which may be unavailable, mismatched to the target data, or insufficiently resolved to capture fine-grained cell subtypes. Reference-free annotation addresses these limitations by inferring cell identities directly from the data. Existing reference-free LLM-based methods usually operate on a fixed clustering partition and rely on conventional marker extraction, limiting adaptive subtype refinement and accurate annotation. To address this limitation, we propose HiLL, a hierarchical LLM-based framework for reference-free cell type annotation. HiLL formulates reference-free annotation as a hierarchical refinement process, using LLM-based split validation to determine when further refinement is warranted and comparative evidence to support accurate annotation. Across human and mouse scRNA-seq and single-cell spatial transcriptomics datasets, HiLL consistently outperforms reference-free LLM baselines, with especially strong gains on fine-grained subtype distinctions. It also remains competitive with reference-based methods and zero-shot foundation models, supporting recursive local refinement as an effective paradigm for reference-free annotation.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
Cell type annotation, Single-cell RNA sequencing, Spatial transcriptomics

Reviews

Among:
Shape:
1234this paper, Top 15%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_TJxHOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

HiLL builds a hierarchy of cell type annotations by recursively clustering cells and asking an LLM whether candidate splits are biologically distinguishable. Comparative marker evidence guides annotation, while semantic regularization links cell and text representations. Different branches can stop at different depths. The experiments cover human pancreas, human brain, and mouse brain datasets, with component ablations and Cell Ontology-based evaluation.

Critical strengths

This method allows different branches to stop splitting at different levels, which matches the varying granularity required in cell annotation. The newly added multi-resolution comparison reuses the same marker-gene extraction pipeline and provides further evidence that the iterative refinement idea is effective. The paper also reports API usage, runtime, and examples of successful and unsuccessful splits, making the overall pipeline clearer.

Critical weaknesses

Although the multi-resolution comparison addresses the attribution issue, the two experiments use different amounts of LLM resources. On the mouse brain dataset, HiLL uses approximately 1.97 times as many calls and 1.92 times as many tokens as the comparison version. It is therefore difficult to determine whether the performance improvement comes from recursive refinement itself or simply from using more LLM computation. This marker-gene selection scheme is more likely to choose genes that distinguish broad cell populations. Its ability to distinguish closely related cell subtypes remains unclear. In addition, the cell ontology curation was performed by only one person, without independent cross-checking or inter-annotator agreement data.

Questions for authors

Given the mismatch in LLM calls and token usage, how much of the performance improvement can be attributed to recursive refinement? Please provide a matched-budget comparison or discuss this limitation explicitly.

How might the single-curator ontology curation affect the reported metrics? If feasible, please conduct an independent review of a small subset of samples.

2 comments
AuthorsOpenReview ↗

Response to the Multi-Resolution Ablation, Actual API/Token Usage, and Runtime

(W1) We thank the reviewer for these thoughtful comments on recursive semantic refinement, its cost, split validation, and marker ranking. We address them in turn below: W1.1 presents the multi-resolution clustering ablation under the same marker summaries; W1.2 discusses API-call and token-usage comparability; W1.3 reports cost and runtime; W1.4 provides representative accepted/rejected split examples; and W1.5 discusses marker ranking among closely related sibling populations as a limitation.

W1.1 (Attribution to recursive semantic refinement itself)

We thank the reviewer for raising this key issue regarding the attribution of recursive semantic refinement. We understand the reviewer’s concern as whether the remaining performance gains indeed arise from recursive semantic refinement itself. To address this, we replaced iterative semantic refinement with multi-resolution clustering in an ablation and compared the two while keeping the construction of marker summaries consistent. The results show that the multi-resolution scheme has slightly lower overall metrics, with a more pronounced gap in macro-F1, indicating that recursive semantic refinement still contributes to fine-grained small categories.The results are as follows:

HP: Human Pancreas; MB: Mouse Brain; Anc: Ancestor; Desc: Descendant.

MethodHP Anc ACCHP Anc F1HP Desc ACCHP Desc F1MB Anc ACCMB Anc F1MB Desc ACCMB Desc F1
HiLL0.9160.5830.7840.4130.9500.7820.9380.735
HiLL(MR)0.8750.5450.7380.3930.9430.7180.9260.683

The multi-resolution scheme is slightly lower than HiLL’s iterative refinement on overall metrics, and the gap is more evident in macro-F1, which better reflects annotation accuracy for small categories. One possible explanation is that the current multi-resolution scheme is less capable than HiLL of perceiving fine-grained clustering across different branches. This ablation has been added to lines 437–442 of the main text and Table 2, with implementation details in Appendix A.15.

W1.2 (API Calls and Token Usage in the Comparison with Multi-Resolution Clustering)

We thank the reviewer for this constructive suggestion regarding a comparison with multi-resolution clustering under the same marker summaries and a matched LLM budget. We agree that such a comparison would be informative. Ideally, it should strictly align the number of calls and token budgets; however, because the hierarchical tree structure and the number of clusters are data-driven, each cluster triggers one LLM call, and the output length varies with the marker set and split decisions, strictly matching budgets is difficult. We therefore report actual API calls and token usage to facilitate the reviewer’s judgment of comparability.. On the mouse brain dataset, the multi-resolution scheme used approximately 976 calls and 1.33 million tokens (593 annotation calls, with input/output of approximately 450k/520k; 383 split-decision calls, with approximately 320k/40k). HiLL used approximately 1,923 calls and 2.55 million tokens (1,327 annotation calls, with approximately 1.00M/1.13M; 596 split-decision calls, with approximately 360k/60k). HiLL’s total calls and token consumption are therefore about 1.97× and 1.92× those of the multi-resolution scheme, while the average token per call is similar between the two (about 1,363 vs. 1,326 tokens/call). The detailed token usage for HiLL is provided in Appendix A.16.

W1.3 (API calls, token usage, and runtime)

We thank the reviewer for reminding us to supplement cost information such as API calls, token usage, and runtime. We have now added cost-related data (Figure 18 and Table 10), including API calls, token usage, and runtime, in the hope that this will help the reviewer judge the actual overhead of the recursive pipeline. Regarding API calls and token usage, although the number of calls varies across the three datasets, the average cost per call is relatively stable (approximately 1,326–1,618 tokens). Annotation dominates token usage, accounting for about 84% of tokens on each dataset, whereas the subcluster stage consumes only about 16%. Token usage also increases with hierarchy depth, with the deepest level accounting for the largest share. Regarding runtime, HiLL averages about 1,045 s (17.4 min) per mouse-brain dataset under a serial configuration; runtime grows with hierarchy depth, and the dominant costs are pairwise DE screening and LLM annotation, both of which are embarrassingly parallel and for which we provide parallel implementations. Full results are reported in Appendix A.16 and A.17, respectively.

AuthorsOpenReview ↗

Response to Split-Validation Examples, Sibling-Marker Ranking, Ontology Curation, and Independent-Review Limitations

W1.4 (Role of split validation and representative accepted/rejected examples)

We thank the reviewer for pointing out that the role of split validation needs more concrete examples. We acknowledge that split validation has only a small effect on the final scores, but we have now added representative examples to illustrate its constraining role in accepting or rejecting populations during the recursive process. The revised Appendix A.13 adds an MSN example: MSNs were identified in the first round; in the second round, a split into drd1 and drd2 groups was produced, and because these two markers are mutually exclusive canonical markers, this split was retained; in the third round, D2-MSNs were split into clusters of 1,486 and 18 cells, and because the latter lacked marker support and had an extremely low size ratio, the LLM rejected this split and merged the redundant subpopulations, thereby avoiding over-splitting. Therefore, its role mainly lies in the mechanistic constraint on accepting or rejecting populations during the recursive process, rather than in substantially improving the final scores. Other influencing factors are also discussed in Appendix A.9.

W1.5 (Marker ranking in closely related sibling populations)

We thank the reviewer for reminding us of the potential bias arising from marker ranking in closely related sibling populations. We agree that this concern is reasonable, and we also noticed this potential bias during our study. Although we attempted to take this factor into account, we have not yet found an effective and low-cost implementation, so this version does not explicitly model the marker-difference relationships among sibling populations. We have noted this as a limitation in the revised Discussion section and plan to further explore it in future work (lines 514–517).

W2.1 (Ontology curation workflow, review of ambiguous mappings, and proportion of manual correction)

We thank the reviewer for raising transparency of manual curation. All methods used the same automatic text-processing pipeline. We did not use LLM outputs directly as standard CL terms; instead, candidate CL terms were generated by automatic mapping and then reviewed item by item by a curator. Ambiguous mappings were filtered out as empty labels during automatic mapping and then manually reviewed and corrected by the curator without knowledge of the method source. Taking mouse brain as an example, exact-match rates between raw outputs and CL text were low (GPTCellType 4%, LICT 2%, scPilot 1%, HiLL 1%); the proportions automatically mapped to CL terms were 83%, 81%, 58%, and 47%, respectively; and the proportions still requiring manual correction after automatic mapping were approximately 39%, 34%, 63%, and 75% (denominator includes empty labels). Details are in Appendix lines 894–908.

W2.2 (Independent review, agreement statistics, and limitations)

We thank the reviewer for pointing out the importance of independent review and agreement statistics. We agree that this concern is reasonable. At present, all manual corrections were completed by the same curator, and independent double review has not yet been conducted; therefore, we cannot currently provide inter-rater agreement statistics or an independently verified proportion of ambiguous mappings. This setup helps maintain consistency in processing across methods, but we recognize that it still lacks independent review. We have listed this as a limitation in the revised manuscript and plan to introduce independent review and agreement statistics in subsequent related studies; the relevant content is in Appendix lines 894–908.

(Q1) We thank the reviewer for this comparison request. This comparison is provided in W1.1–W1.2: W1.1 reports the multi-resolution ablation under the same marker-summary construction, and W1.2 reports actual API calls and token usage for budget comparability. Because hierarchy and cluster numbers are data-driven, strictly matching the LLM budget is difficult; on mouse brain, HiLL uses about 1.97× the calls and 1.92× the tokens of multi-resolution, with similar average tokens per call (about 1,326 vs. 1,363). Full results are in Table 2, lines 437–442, and Appendix A.15–A.16.

(Q2) We thank the reviewer for this clarification request and appreciate the concern regarding the transparency of the ontology evaluation. This is addressed in W2.1–W2.2: all methods used the same automatic pipeline; ambiguous mappings were filtered as empty labels and then manually reviewed by a curator blinded to method source. On mouse brain, the proportions still requiring manual correction after automatic mapping were approximately 39%, 34%, 63%, and 75% for the four methods. Full details are in W2.1–W2.2 and Appendix lines 894–908.

Reviewer_FvQ4OpenReview ↗
Rating
4(+1)
Confidence
4
Informativeness
2
Presentation
3
Soundness
3
Read review
Paper summary

HiLL proposes a reference-free framework for cell-type annotation through recursive clustering. An LLM validates candidate splits and generates labels and descriptions from level-wide marker evidence. These descriptions then regularize the expression representation used in subsequent refinement rounds. The paper reports promising results on human pancreas, human brain, and mouse brain data.

Critical strengths
  1. The problem is well motivated. Different cell populations may require different annotation depths, making recursive refinement a reasonable alternative to a single global partition. The method does not require target annotations or an external labeled expression reference.

  2. The main design choices have empirical support. The ablations show benefits from recursive refinement and level-wide pairwise marker extraction. These are the most convincing contributions of the paper.

  3. The experimental coverage is reasonably broad. The evaluation includes multiple species and both single-cell and spatial transcriptomics data. Component ablations, repeated seeds, and comparisons across language-model backends help clarify performance and stability.

Critical weaknesses
  1. The evaluation does not adequately establish fine-grained correctness. Hierarchical matching gives full credit to predictions that are subtypes of the reference label, although a coarse reference cannot verify a specific subtype. Figure 14, for example, splits the reference label “neuron” into several predicted subtypes, demonstrating finer output rather than necessarily correct subtype assignments.

  2. Semantic alignment lacks independent validation. Greater agreement with descriptions used during training does not establish biological correctness. Independent tasks and tests of error reinforcement would strengthen the evidence.

  3. Language-Cell Pre-training for Cell Identity Understanding (ICML 2024) supports zero-shot annotation through cell–text alignment. It should be discussed, with its distinction from open-vocabulary generation made clear, and considered as a baseline on applicable datasets.

  4. The added value over stronger LLMs remains unclear. Although the appendix compares several backends, stronger models such as GPT-6-astra and Fable-5.1 should also be considered, with the full HiLL pipeline compared against simple prompting or iterative annotation using the same backend. Such controls would establish whether the additional design choices still provide worthwhile gains as model capabilities improve, accounting for both accuracy and computational cost.

Questions for authors

See the Weaknesses.

6 comments
AuthorsOpenReview ↗

Response to Validation Concerns on Fine-Grained Subtype Correctness and Semantic Alignment

(W1) We sincerely thank the reviewer for this valuable comment. We agree that fine-grained subtype recognition performance is an important aspect of evaluating HiLL and a valuable direction pointed out by the reviewer. We would like to clarify that the labels in the current mouse and human brain datasets do not provide fine-grained subtype ground truth, making it difficult to directly evaluate the correctness of subtype-level predictions. To provide indirect evidence under the available data conditions, we used point-biserial correlation analysis to examine the association between predicted subtypes and their corresponding markers.

Taking the multiple subtypes in Figure 14 as an example, the statistical significance between the four human brain InN subtypes and their corresponding markers all reached p < 0.001, with correlation coefficients of 0.67 for LAMP5, 0.72 for PVALB, 0.83 for SST, and 0.85 for VIP. In addition, in the mouse brain dataset, we also observed significant correlations between different neuronal subtypes and specific markers. We regard these results as auxiliary support for the plausibility of subtype annotation. We have added the above analyses to lines 374–377 of the main text and Appendix A.12 and provided point-biserial correlation heatmaps between predicted subtypes and their corresponding markers in human brain and mouse brain (Appendix Figures 16–17).

(W2) We thank the reviewer for this constructive comment. We agree with the reviewer’s concern that greater agreement with descriptions used during training alone is insufficient to demonstrate that semantic alignment is biologically correct.

To this end, we have strengthened the relevant evidence in the revision from two aspects. On the one hand, we further clarified the positioning of the independent unseen-text retrieval experiment already present in the main text as an independent-task validation. In this experiment, the aligned cell embeddings achieved an MRR of 0.59, compared with 0.38 for the unaligned baseline. On the other hand, we added a text–cell mismatched pairing control group; under the same evaluation pipeline, the MRR dropped to 0.27, lower than the unaligned baseline. These two results provide auxiliary evidence from the perspectives of independent-task validation and error reinforcement testing, respectively.

Specifically, the unseen-text retrieval experiment based on Cell Ontology in Section 4.4 already existed in the original submission; in this revision, we more clearly explain its purpose as an independent-task validation. In this experiment, Cell Ontology descriptions were embedded but did not participate in training. When retrieval was performed using the aligned cell embeddings, the MRR was 0.59, compared with 0.38 for the unaligned baseline, indicating that the aligned embeddings can effectively retrieve unseen text rather than merely fitting the descriptions used during training. To further address the concern regarding error reinforcement, we added a mismatched pairing control group: during training, the pairing between text and cells was shuffled, while the model architecture, data scale, and training strategy were kept unchanged. Under the same evaluation pipeline, the MRR dropped to 0.27, lower than the unaligned baseline. We regard this result as auxiliary evidence that retrieval performance depends on the correct text–cell correspondence, rather than being driven solely by text embeddings or model capacity. Accordingly, we have revised Figure 3 and lines 463–473 of the main text.

AuthorsOpenReview ↗

Response to the LangCell and Stronger LLM Backend Concerns

(W3) We thank the reviewer for this valuable suggestion. We agree that it is necessary to discuss LangCell in the main text and to clarify its distinction from open-vocabulary generation; we have included it as a baseline in comparisons. Specifically, LangCell’s zero-shot capability differs from the LLM-based open-vocabulary generation paradigm: it performs retrieval-based annotation through cell–text alignment, and the candidate cell types and their descriptions need to be pre-specified, thus making it closer to retrieval-based annotation within a given candidate description set rather than open-vocabulary generation without candidate restrictions. Generation methods such as GPTCellType and HiLL do not require a pre-specified candidate list. Therefore, LangCell’s “openness” is mainly openness within a given description set. We also noted two limitations of this mechanism in application.

First, reference-set dependence: annotation is limited to manually specified candidates. Second, species coverage limitation: LangCell was pre-trained on human data, and applying it to mouse brain requires gene mapping, which may lead to performance degradation. To evaluate its retrieval-based zero-shot performance, we constructed a candidate pool using the Cell Ontology descriptions of all cell types in each dataset, and we cautiously regard this result as a performance upper bound under this setting rather than generalization performance in practical open scenarios. On the three datasets, the results of LangCell are as follows:

--Human Pancreas AccHuman Pancreas F1Human Brain AccHuman Brain F1Mouse Brain AccMouse Brain F1
Ancestor0.6200.5230.9960.8390.1330.309
Descendant0.6050.5060.9960.8390.1330.309

The results show that on human data, LangCell outperforms open methods such as GPTCellType at the Descendant level; compared with HiLL, it is relatively lower on human pancreas and performs better on human brain; on mouse brain, performance drops noticeably after gene mapping, whereas HiLL and LLM-based methods do not rely on such cross-species gene mapping. The relevant results have been incorporated into Table 1, and methodological discussion and implementation details have been added to lines 103–107 of the main text and Appendix A.1.1.

(W4) We thank the reviewer for this constructive comment. We agree that comparing backends only in the appendix is insufficient, so we add GPT-6-Astra experiments on mouse brain and compare HiLL with GPTCellType (as simple prompting) under the same backend, reporting accuracy and cost.

BackendMethodAncestor ACCAncestor F1Descendant ACCDescendant F1Token (input/output)Cost
DeepSeek-flashHiLL0.9500.7820.9380.735~2550k (1359k/1191k)~0.85–1.70
DeepSeek-flashGPTCellType0.8820.7070.7040.598----
GPT6-AstraHiLL0.9600.7870.9480.778~4049k (1373k/2676k)~147.5
GPT6-AstraGPTCellType0.9560.7210.9020.693~87k (84k/3k)~0.99

On mouse brain data, replacing the GPTCellType backend from DeepSeek-flash with GPT-6-Astra improved Ancestor accuracy/macro-F1 from 0.882/0.707 to 0.956/0.721, and Descendant from 0.704/0.598 to 0.902/0.693, indicating that a stronger backend with simple prompting can also bring considerable improvements. Under the same GPT-6-Astra backend, HiLL achieved Ancestor accuracy of 0.960, not significantly different from GPTCellType’s 0.956 in the Wilcoxon test; however, HiLL’s Ancestor macro-F1 was 0.787 (vs. 0.721), Descendant accuracy was 0.948 (vs. 0.902), and Descendant macro-F1 was 0.778 (vs. 0.693). Except for Ancestor accuracy, the other three metrics reached statistical significance (p < 0.05). Thus, even with a stronger model, HiLL still tends to maintain advantages in fine-grained and macro-averaged metrics, while Ancestor accuracy is close to saturation in this setting.

Regarding cost, assuming no cache hits and using official pricing, GPTCellType + GPT-6-Astra consumes approximately 87k tokens and costs about USD 0.99; HiLL + DeepSeek consumes approximately 2550k tokens, costing about USD 1.70 and 0.85 under peak and off-peak pricing, respectively. HiLL + GPT-6-Astra consumes 4049k tokens and costs about USD 147.5, i.e., approximately 87–174 times HiLL + DeepSeek based on actual costs, while the relative performance gain is mainly reflected in Descendant macro-F1 (+0.043). In contrast, HiLL + DeepSeek and GPTCellType + GPT-6-Astra are in the same order of magnitude in cost, but the former achieves Descendant accuracy/macro-F1 of 0.938/0.735 versus 0.902/0.693, and Ancestor macro-F1 of 0.782 versus 0.721, with Ancestor accuracy only 0.006 lower. These results indicate that HiLL shows a certain advantage in the cost–performance trade-off. The above analysis has been added to Appendix A.14.

Thanks to the author's reply, most of my concerns have been resolved. However, I think the subtype issue mentioned by W1 can be further verified, such as looking for some datasets with subtype annotations to supplement experiments.

Reviewer_yvn2OpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

HiLL performs reference-free cell type annotation through recursive refinement. It proposes local cluster splits, asks an LLM to check their biological support, and uses pairwise marker comparisons across the current level to generate labels and descriptions. These descriptions also guide later representation learning. Experiments on pancreas and brain datasets show improvements over the tested reference-free LLM methods. The ablations attribute most gains to recursive refinement and marker extraction, while split validation and semantic regularization have smaller effects on annotation quality.

Critical strengths
  • The motivation is clear: choosing annotation granularity and choosing marker evidence should be considered together. Using sibling comparisons for split decisions and broader comparisons for labeling is a sensible response to that problem.
  • The marker ablation shows a clear practical benefit, and recursive refinement improves class-balanced annotation. The paper also acknowledges that semantic regularization is not the main source of the annotation gains.
Critical weaknesses
  • The evaluation does not clearly establish correct fine subtype recovery. Descendant matching can count a fine prediction as correct against a coarse reference label. Figure 2 mainly checks marker consistency, and its human-brain panel appears mislabeled: the VIP row has strongest SST expression, while the LAMP5 row has strongest VIP expression. This makes the central subtype evidence hard to trust as presented.
  • The extra value of LLM-controlled granularity is not well established. Table 2 shows little annotation benefit from split validation, while most gains come from marker extraction and repeated clustering. Existing reference-free work such as CASSIA already supports joint annotation of subclusters, so the paper needs a clearer account of what the adaptive split decisions add beyond that workflow.
Questions for authors
  1. Are the row labels in Figure 2A permuted? Please clarify the intended label-to-marker correspondence and provide the corrected panel if needed.
  2. Which reported results check the predicted fine subtypes against labels at the same resolution, rather than accepting their coarse ancestor? Please explain using the existing annotations and evaluation mappings.
  3. Does split validation mainly merge redundant groups, or does it change which biologically distinct populations are retained? An existing accepted/rejected split example would help explain its contribution beyond recursive subclustering.
6 comments
AuthorsOpenReview ↗

Response to Figure 2A Correction, Fine Subtype Evaluation, and Split Validation Example

(W1) We are very grateful to the reviewer for drawing our attention to this issue. We sincerely apologize that this was indeed an oversight on our part during figure preparation: when manually assembling multiple subpanels in Figure 2, the labels in panel A were misplaced. We have corrected Figure 2 in the revised main text. Regarding the marker distributions of the subtypes and our predicted subtypes, the actual expression patterns themselves are clear. In addition, we report point-biserial correlation analyses between the predictions for these four subtypes and the corresponding markers: all p values were < 0.001, with effect sizes of 0.41 for LAMP5, 0.67 for PVALB, 0.84 for SST, and 0.81 for VIP. Furthermore, our considerations regarding further evaluation of fine subtypes are explained in our response to Q2.

(W2) We thank the reviewer for this valuable comment. We understand that the role of split validation is not limited to merging redundant groups; rather, it has a dual function. Through split validation, it can remove continuous states and overly small subpopulations, while also accepting, retaining, and distinguishing genuinely distinct biological populations.

Here we illustrate this using medium spiny neurons (MSNs) in the mouse brain. When cluster 1 was identified as MSNs and further divided, a Drd1/Drd2 separation emerged; because Drd1 and Drd2 are mutually exclusive canonical markers of MSNs, this split was retained as a biologically distinct population. In the subsequent subdivision of D2-MSNs, the population was divided into clusters of 1,486 and 18 cells. The 18-cell subpopulation lacked marker support and represented an extremely low proportion, so the LLM rejected this split and merged the redundant subpopulations, avoiding over-segmentation. This representative case has been added to Appendix A.13. In addition, Appendix A.9 provides a broader analysis showing that LLM-controlled splitting reduces the generation of overly small clusters, further supporting its value beyond this illustrative example.

(Q1) We thank the reviewer for bringing this to our attention. As noted in W1, the apparent label misalignment in Figure 2A was caused by misplaced labels during our manual assembly of multiple subpanels, rather than by an error in the correspondence between labels and markers themselves. We apologize for the confusion this caused and have corrected Figure 2A. After correction, the subtype labels are aligned with the expression of the corresponding markers. The relevant marker correlation results are reported in W1.

(Q2) We thank the reviewer for this valuable comment. We believe that the human pancreas dataset used in this study can provide results for “predicted fine subtypes against labels at the same resolution,” because the cell-type labels in this dataset have largely been refined to the subtype level, including multiple endocrine cell subtypes and T-cell subtypes in the pancreas. This is also reflected in the human pancreas annotation results shown in Table 1: when the matching criterion for comparison becomes stricter (from ancestor to descendant), the performance of HiLL on human pancreas decreases more markedly, whereas the performance changes relatively little on human brain and mouse brain, which have coarse ground truth labels. We have added and explained this phenomenon and its causes in lines 363–370 of the revised manuscript.

In addition, to further directly support the validity of subtype identification in human brain and mouse brain, we added further analyses of cell subtypes in human brain and mouse brain. Since human brain and mouse brain do not provide ground truth subtype labels, we indirectly support the subtype validity of the annotation results by analyzing point-biserial correlations between predicted subtypes and their corresponding markers. We generated point-biserial correlation heatmaps between these predicted neuronal subtypes and markers, shown in new Appendix Figures 16 and 17; the predicted results show clear associations with the corresponding cell-type markers. We have updated lines 374–377 of the manuscript and Appendix A.12 to explain the validity of HiLL in identifying subtypes.

(Q3) We thank the reviewer for this question. As noted in W2, split validation is not limited to merging redundant groups; it also accepts and retains genuinely distinct biological populations while rejecting splits that lack marker support or are overly fine. In the mouse brain MSN example, the Drd1/Drd2 separation was retained because it corresponds to mutually exclusive canonical markers, whereas the subdivision within D2-MSNs containing only 18 cells and lacking marker support was rejected and merged. We have added this accepted/rejected example to Appendix A.13 to illustrate the additional value of LLM-controlled granularity splitting compared with recursive sub clustering.

I appreciate the authors' effort on rebuttal. I think the answer partially resolve my concerns. Regarding the splitting validation, what specific validation criterias are used to prompt LLM to make split decisions? Do different LLMs have different levels of threshold? I agree with Reviewer FvQ4 that it is unclear whether a stronger LLM would benefit more on this task compared to the iterative method proposed in the manuscript.

AuthorsOpenReview ↗

Response to the split validation criteria and threshold differences across LLMs

We thank the reviewer for the positive assessment of our rebuttal work, and we also thank the reviewer for pointing out that the original manuscript did not sufficiently explain the role of the LLM in split validation. We apologize for this, and we have now added evaluation details for split validation, in response to the reviewer’s concern about a stronger LLM backend, we have added corresponding response.

(1) Specific criteria used by the LLM in split validation: We would like to clarify that the LLM performs semantic validation of the candidate partitions produced by the metric-based proposal and makes a binary “split/not split” decision. Our method does not use an explicit numerical threshold filter. The LLM’s decision is mainly based on whether the marker differences between candidate subclusters indicate discrete cell identities, such as different cell types or subtypes, rare subtypes, or contaminants. Clustering metrics serve as a secondary reference to help rule out clearly noise-driven partitions. If the evidence is insufficient or ambiguous, we adopt a conservative strategy: no split is made, the parent cluster remains unsplit, and further refinement of that branch stops. Specifically, the decision criteria in the prompt can be summarized as follows:

1.Support splitting: the subclusters show distinct, non-redundant marker genes indicating separate cell populations, such as rare subtypes or contaminants.

2.Do not support splitting: the marker differences are more likely explained by continuous states, such as cell cycle, stress, or metabolic gradients, rather than discrete cell-type identity.

3.When uncertain, default to not splitting, unless the markers clearly indicate an independent cell population.

The specific input format, prompt design, and implementation details are in the supplementary material and Appendix A.18.

(2) Whether different LLMs have different thresholds. As noted above, our method does not use an explicit numerical threshold, so there is no issue of tuning a separate threshold for different models. The LLM makes semantic judgments based on marker differences between candidate subclusters; when the evidence is insufficient or difficult to judge, the default is not to split. We agree that different LLMs may differ in how they judge whether the evidence is sufficient. More precisely, this difference reflects an implicit difference in conservativeness rather than an explicit threshold. To examine this, using exactly the same prompt, we replaced the original DeepSeek backend with GPT-6-Astra and re-evaluated the same set of candidate partitions. For the decisions made by the LLM in the original pipeline (512 for mouse brain and 191 for human pancreas), the results are as follows:

MetricMouse brainHuman pancreas
Total decisions512191
Agreement444144
Disagreement6847
Agreement rate86.7%75.4%
Disagreement: rejected existing split5343
Disagreement: accepted originally unsplit154
DatasetMetricDeepSeekGPT6-Astra
Mouse brainARI0.5720.572
Mouse brainV-measure0.7720.774
Human pancreasARI0.6340.676
Human pancreasV-measure0.7540.786

“Agreement” includes cases where both backends split and where neither split. Most disagreements were cases where GPT-6-Astra rejected a split originally made by DeepSeek (mouse 53/68, human 43/47), suggesting that GPT-6-Astra is generally more conservative; it also accepted a few originally unsplit parents (mouse 15, human 4), indicating that it does not apply a blanket rule. After replacement, the final partitions remained largely stable (mouse ARI 0.572 → 0.572, V-measure 0.772 → 0.774; human ARI 0.634 → 0.676, V-measure 0.754 → 0.786), with Purity essentially unchanged. These results suggest that the replacement mainly adjusts conservativeness on ambiguous cases rather than overturning clear splits.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.