The Landscape of Ferroptosis-Related Gene Signatures as Molecular Stratification in Triple-Negative Breast Cancer

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The manuscript “Ferroptosis-Related Gene Signatures as Potential Diagnostic and
Prognostic Markers in Triple-Negative Breast Cancer” conduct transcriptomic and proteomic analyses of different subtypes of triple-negative breast cancer by using publicly available datasets. It is demonstrated that basal-like triple-negative breast cancer is the most sensitive to ferroptosis compared with other subtypes, and that AR and EZH2 are considered important factors related to ferroptosis in breast cancer. I only have a few comments on this manuscript.

1. The author should explain the rationale behind filtering data from these different transcriptomic datasets for analysis.
2. The author neither attempted to verify at least some of the results nor discussed whether it is necessary to repeat the research to confirm its universality.
3. The clarity of both the text and the supplementary material pictures can be improved. Besides, there are issues such as incomplete legends in Figure S1 and overwritten names of signal pathways in Figure S5C.
4. Introduction can be strength by illustrating the current status of bioinformatics analysis of ferroptosis. This will enrich the context. Journal of Controlled Release, 2025, 379: 866-878. Exploration. 2025, 5(1): 20240002.

Author Response

Reviewer 1

Responses to Reviewer 1:

We thank the Reviewer for the constructive comments and valuable suggestions, which have helped us improve the clarity, rigor, and contextualization of our manuscript. Our point-by-point responses are provided below.

Comment 1: 1. The author should explain the rationale behind filtering data from these different transcriptomic datasets for analysis.

Response:

We thank the Reviewer for this comment. The rationale for dataset filtering was to ensure consistency, comparability, and biological relevance across heterogeneous transcriptomic cohorts. Specifically, only samples with complete molecular subtype annotation, gene expression data, and available survival information were included in downstream analyses. This approach minimized confounding effects arising from missing data, platform-specific noise, or incomplete clinical annotation. We have clarified this rationale in the Materials and Methods section to explicitly describe the filtering criteria applied to the METABRIC, TCGA, and GEO datasets. These changes have been introduced on page 5, Section 2. (Data set collection and filtering), paragraph 2, lines 170-177.

Comment 2: The author neither attempted to verify at least some of the results nor discussed whether it is necessary to repeat the research to confirm its universality.

Response:

We agree with the reviewer that experimental verification and independent repetition are essential to confirm the universality of in silico findings. While the present study was designed as a comprehensive computational analysis, we emphasized in the Discussion that further experimental validation and repetition in additional cohorts will be required to verify the robustness and universality of the results. This limitation and future perspective are now more clearly articulated in the revised manuscript. We have revised the last sentence on page 27, Section 4 (Discussion, Limitations), paragraph 6, lines 885-886 and page 28, Section 4 (Discussion, Limitations), paragraph 1, lines 887-902.

Comment 3: The clarity of both the text and the supplementary material pictures can be improved. Besides, there are issues such as incomplete legends in Figure S1 and overwritten names of signal pathways in Figure S5C.

Response:

We thank the reviewer for pointing out this issue. The text has been carefully revised to improve clarity and readability throughout the manuscript. In addition, all supplementary figures have been re-examined and corrected. Incomplete legends have been expanded (including Figure S1, S5 and S6), and graphical issues such as overwritten pathway names in Figure S5C and 5D have been resolved.

Comment 4: Introduction can be strength by illustrating the current status of bioinformatics analysis of ferroptosis. This will enrich the context. Journal of Controlled Release, 2025, 379: 866-878. Exploration. 2025, 5(1): 20240002.

Response:
We appreciate this valuable suggestion. The Introduction has been expanded to better contextualize the current state of bioinformatics-driven ferroptosis research. We have incorporated recent, relevant studies on computational approaches to ferroptosis regulation and therapeutic targeting, including references suggested by the Reviewer (Journal of Controlled Release, 2025; Exploration, 2025). This addition strengthens the conceptual framework and better positions our study within the evolving landscape of ferroptosis-focused bioinformatics research. These changes have been introduced on page 3, Section 1 (introduction), paragraph 3, lines 117-132.

As additional references were added to strengthen the Introduction, the numbering of subsequent references has been adjusted accordingly throughout the manuscript.

Reviewer 2 Report

Comments and Suggestions for Authors

The number of breast cancer patients are increasing worldwide. Among breast cancer histological subtypes, triple-negative breast cancer (TNBC) is resistant to hormone therapy and antibody drug. Currently, TNBC clinically hardest cancer to achieve complete cure. This manuscript report the transcriptome analyses, unfortunately, it is too descriptive and did not prepare integrally.

 

Major points

#1; Authors use ‘normal-like tumors’ to contrast basal-like. This ‘normal-like tumor’ is confusing due to name cancer subtypes. Please rename this terminology.

 

#2: Figure 8 Ferroptosis Index is hard to understand. How did you determine? It seems to be no difference among luminal A, B and HER2.

 

#3: Figure 9 shows mRNA levels of ferroptosis-related genes. However, Figure 1 shows mRNA levels. What is the difference?

 

Author Response

Reviewer 2

Responses to Reviewer 2

We thank the Reviewer for the critical evaluation of our manuscript and for the constructive comments, which helped us improve clarity, terminology, and presentation of the results. Our detailed responses are provided below.

Major Comment 1: Authors use ‘normal-like tumors’ to contrast basal-like. This ‘normal-like tumor’ is confusing due to name cancer subtypes. Please rename this terminology.

Response:
We agree with the Reviewer that the term “normal-like tumors” may be confusing, as it does not represent truly normal breast tissue but rather a PAM50-defined intrinsic subtype. To avoid ambiguity, we have clarified in the manuscript that “Normal-like” refers specifically to the PAM50 Normal-like intrinsic breast cancer subtype, and not to healthy breast tissue within the METABRIC cohort.

Although the PAM50 Normal-like subtype has been used in some studies as a proxy for normal breast tissue due to its transcriptional similarity, it represents a tumor-intrinsic subtype rather than true non-malignant tissue. In the present study, Normal-like samples were not used as normal tissue controls. Instead, they were analyzed as a PAM50-defined intrinsic breast cancer subtype characterized by relatively low proliferative activity and a transcriptional profile closer to non-proliferative states. In this context, the Normal-like subtype was used as a comparator to Basal-like tumors to contrast highly aggressive, proliferative ferroptosis-associated programs against less proliferative tumor states within breast cancer heterogeneity, rather than to represent non-malignant tissue.

These changes have been introduced on page 5, Section 2.1 (Data set collection and filtering), paragraph 1, lines 167-169.

Major Comment 2: Figure 8 Ferroptosis Index is hard to understand. How did you determine? It seems to be no difference among luminal A, B and HER2.

Response:
We thank the Reviewer for highlighting the need for a clearer methodological description of the Ferroptosis Index (FI). After revision, this is now Figure 9. We have expanded the Materials and Methods section to explicitly describe how FI was constructed, the origin of β-coefficients, and the intended interpretation of FI as a descriptive measure of ferroptosis-associated transcriptional potential rather than evidence of ongoing ferroptotic cell death. We also clarified that FI was calculated exclusively within the METABRIC cohort and used to assess relative enrichment across intrinsic subtypes, which explains the modest differences observed among Luminal A, Luminal B, HER2-enriched, and Normal-like tumors. These changes have been introduced on page 7, paragraph 1, lines 246-253, page 16, Section 3.4. (Ferroptosis Index Analysis) paragraph 2, line 533; page 16, Section 3.4. (Ferroptosis Index Analysis) paragraph 3, line 541; and page 25, Section 4. (Discussion) paragraph 5, lines 790-793.

Major Comment 3: Figure 9 shows mRNA levels of ferroptosis-related genes. However, Figure 1 shows mRNA levels. What is the difference?

Response:
We appreciate the Reviewer for pointing out this potential source of confusion. After revision, Figure 1 is Figure 2, and Figure 9 is Figure 10. The distinction between the two figures has now been clarified in Figure 10. legend. Figure 2 presents a global heatmap-based comparison of ferroptosis-related gene expression patterns between Basal-like and Normal-like intrinsic subtypes, highlighting overall clustering and differential expression trends. In contrast, Figure 10 focuses on the quantitative expression levels of selected subset of ferroptosis-related genes that were prioritized for downstream analyses, including Ferroptosis Index (FI) calculation. These genes represent both established ferroptosis drivers and suppressors, span multiple ferroptosis-associated pathways, integrating survival-associated differentially expressed genes with well-established ferroptosis markers, and were selected based on their β-coefficients and biological relevance. Thus, Figure 10 serves a targeted, gene-level interpretative role that complements the global expression overview shown in Figure 2. To improve clarity, we have revised the legends and explicitly described the complementary roles of these figures in the manuscript. These changes have been introduced on page 18, paragraph 1 (Figure legend), lines 579-584.

Reviewer 3 Report

Comments and Suggestions for Authors

This is a comprehensive multi-omics analysis of ferroptosis-related programs in TNBC, integrating bulk transcriptomics, proteomics, and single-cell data. The work is technically strong and biologically coherent, and the focus on Basal/TNBC is appropriate. However, the clinical utility of the prognostic model is limited by modest discrimination, and several conceptual and methodological issues should be addressed to strengthen translational relevance.

1) Prognostic model performance and clinical relevance

The reported AUC of ~0.56 in the METABRIC cohort indicates limited prognostic discrimination, only marginally better than chance. This substantially weakens claims of “robust” prognostic utility.

The authors should temper conclusions and clearly distinguish biological signal discovery from clinically actionable risk stratification.

Consider benchmarking the ferroptosis signature against established clinical variables (stage, grade) and existing TNBC signatures to demonstrate incremental prognostic value.

2) Risk model overfitting and validation

The LASSO model is trained and optimized in METABRIC, but external validation is inconsistent (non-significant in GEO, borderline in TCGA).

The manuscript would benefit from:

Reporting optimism-corrected performance or internal cross-validation.

Clarifying whether coefficients were re-fit or locked during validation.

Claims of generalizability should be softened.

3) Interpretation of ferroptosis “activation”

Elevated FI is interpreted as “ferroptotic potential,” yet high FI is also associated with poor prognosis, which may reflect aggressive proliferation, hypoxia, and metabolic stress, not ferroptotic cell death per se.

The authors should more explicitly acknowledge that FI likely captures a stress-adapted, ferroptosis-poised but not ferroptosis-executing state.

This distinction is critical for therapeutic translation.

4) AR and EZH2 as central regulators

AR downregulation and EZH2 upregulation are well-known hallmarks of Basal/TNBC biology.The authors should clarify what is novel about their role specifically in ferroptosis regulation rather than general subtype identity.

Mechanistic speculation (e.g., EZH2-mediated repression of antioxidant pathways) should be clearly labeled as hypothesis-generating.

 

 

Author Response

Reviewer 3

Responses to Reviewer 3

We sincerely thank the Reviewer for the careful evaluation of our manuscript and for the constructive comments, which helped us improve the clarity, rigor, and conceptual precision of the study. All comments have been addressed as detailed below.

Major Comment 1. Prognostic model performance and clinical relevance. The reported AUC of ~0.56 in the METABRIC cohort indicates limited prognostic discrimination, only marginally better than chance. This substantially weakens claims of “robust” prognostic utility. The authors should temper conclusions and clearly distinguish biological signal discovery from clinically actionable risk stratification. Consider benchmarking the ferroptosis signature against established clinical variables (stage, grade) and existing TNBC signatures to demonstrate incremental prognostic value.

Response:
We agree with the Reviewer that the modest AUC values indicate that the proposed signature should not be interpreted as a standalone clinical prognostic tool. Accordingly, we have revised the manuscript to temper claims regarding predictive robustness and clinical utility.

Specifically, in the Section 3.2.2 (Construction and evaluation of ferroptosis-associated transcriptional stratification model- revised subtitle), we now explicitly state that the model demonstrates modest discriminatory performance and primarily captures biologically relevant differences in survival rather than providing definitive clinical prediction. These changes have been made on page 12, paragraph 2, lines 423-435, page 13, paragraph 2 and page 14, paragraph 1, lines 449-466. In the Discussion, we further clarify that the model represents a ferroptosis-associated stratification framework reflecting transcriptional states linked to overall survival in Basal-like breast cancer, rather than an independent clinical predictor. These changes have been introduced on page 24, paragraph 2, lines 735-745, and page 25, paragraph 1, lines 746-748.

With respect to benchmarking against established clinicopathological variables or existing TNBC gene signatures, we agree that such analyses would be required to demonstrate incremental prognostic value in a clinical prediction setting. However, the primary aim of the present study was not to develop a clinically optimized risk model, but to identify and characterize ferroptosis-associated transcriptional programs linked to tumor overall survival and aggressiveness in Basal-like breast cancer. Accordingly, direct benchmarking against stage, grade, or existing prognostic signatures was considered beyond the scope of this biologically focused analysis and is now acknowledged as an important direction for future work. These clarifications have been added in the limitations of the study on page 27, paragraph 6, lines 885-886 and page 28, paragraph 1, lines 887-902.

Major Comment 2. Risk model overfitting and validation. The LASSO model is trained and optimized in METABRIC, but external validation is inconsistent (non-significant in GEO, borderline in TCGA). The manuscript would benefit from: Reporting optimism-corrected performance or internal cross-validation. Clarifying whether coefficients were re-fit or locked during validation. Claims of generalizability should be softened.

Response:

We acknowledge the Reviewer’s concern regarding potential overfitting and limited external validation. To address this, we have clarified the evaluation strategy and its limitations in the Section 3.2.2 (Construction and evaluation of ferroptosis-associated transcriptional stratification model- revised subtitle) and Discussion. Model coefficients were derived from the METABRIC cohort and applied unchanged to the TCGA and GEO datasets without retraining. We explicitly state that external validation should therefore be interpreted as supportive rather than confirmatory, particularly given differences in cohort size, composition, and statistical power. Internal cross-validation or optimism-corrected performance was not performed, as the primary aim of the model was biological stratification rather than predictive optimization. This limitation and the need for further validation are now explicitly acknowledged. These clarifications have been added on page 12, paragraph 2, lines 423-435. Also in the Discussion section, the limitations of the study on page 27, paragraph 6, lines 885-886 and page 28, paragraph 1, lines 887-902.

 

Major Comment 3. Interpretation of ferroptosis “activation”. Elevated FI is interpreted as “ferroptotic potential,” yet high FI is also associated with poor prognosis, which may reflect aggressive proliferation, hypoxia, and metabolic stress, not ferroptotic cell death per se. The authors should more explicitly acknowledge that FI likely captures a stress-adapted, ferroptosis-poised but not ferroptosis-executing state. This distinction is critical for therapeutic translation.

Response:
We fully agree with the Reviewer that the Ferroptosis Index does not measure active ferroptotic cell death. We have revised Section 3.4 and Discussion to explicitly clarify that FI reflects a ferroptosis-associated transcriptional and metabolic stress state, representing the balance between pro- and anti-ferroptotic gene expression rather than execution of ferroptosis. We have expanded the Materials and Methods section to explicitly describe how FI was constructed, the origin of β-coefficients, and the intended interpretation of FI as a descriptive measure of ferroptosis-associated transcriptional potential rather than evidence of ongoing ferroptotic cell death. These changes have been introduced on page 7, paragraph 1, lines 246-253, page 16, Section 3.4. (Ferroptosis Index Analysis) paragraph 2, line 533; page 16, Section 3.4. (Ferroptosis Index Analysis) paragraph 3, line 541; and page 25, Section 4. (Discussion) paragraph 5, lines 790-793.

Major Comment 4. AR and EZH2 as central regulators. AR downregulation and EZH2 upregulation are well-known hallmarks of Basal/TNBC biology. The authors should clarify what is novel about their role specifically in ferroptosis regulation rather than general subtype identity. Mechanistic speculation (e.g., EZH2-mediated repression of antioxidant pathways) should be clearly labeled as hypothesis-generating.

Response:
We thank the Reviewer for this important point and fully agree. We do not propose AR or EZH2 as novel subtype markers. Instead, the novelty of our study lies in positioning these well-established TNBC-associated factors within a ferroptosis-associated regulatory framework. In the Discussion, we now explicitly state that our integrative analyses suggest AR and EZH2 define distinct ferroptosis-related transcriptional states linking hormone signaling and epigenetic regulation to redox balance and ferroptosis susceptibility, rather than merely reflecting subtype identity. Furthermore, all proposed mechanistic links, such as EZH2-mediated modulation of antioxidant defense or lipid metabolism, are clearly labeled as hypothesis-generating, based on transcriptomic integration and prior literature, and not as direct functional validation within this study. These changes have been introduced on page 27, paragraph 3, lines 866-874.

Reviewer 4 Report

Comments and Suggestions for Authors

This article presents a thorough multi-omics investigation of ferroptosis-related genes in triple-negative breast cancer (TNBC), combining transcriptomic, proteomic, and single-cell RNA sequencing data to discover prognostic signatures and characterize ferroptosis-associated molecular pathways. The work is ambitious, data-rich, and answers a biologically and clinically important topic. The integration of METABRIC, TCGA, GEO, CPTAC, and scRNA-seq datasets is a significant strength. However, various methodological, interpretational, and conceptual concerns must be clarified or improved before the manuscript may be considered for publication. Claims on diagnostic efficacy, prognostic model robustness, confounder handling, and translational interpretation of the Ferroptosis Index (FI) in particular need to be carefully revised.

Major comments:

1. Diagnostic versus Prognostic Claims The article contains multiple mentions to diagnostic relevance; nonetheless, the research findings (Cox regression, LASSO modeling, survival analysis, and FI stratification) suggest prognostic rather than diagnostic utility. There are no explicit diagnostic metrics available (such as classification ROC or sensitivity/specificity). The authors should make a clear distinction between diagnostic and prognostic statements, or modify the title and text accordingly.
   2. ⁠Lack of multivariable survival adjustment Despite the presence of important clinicopathological factors (age, stage, grade, nodal status, and treatment), survival analyses are primarily conducted using univariate Cox regression. It's uncertain whether the hypothesized gene signature and the Ferroptosis Index are independent prognostic variables. Multivariable Cox models or a good explanation for their absence are required.
   3. ⁠The prognostic model has modest predictive performance. The presented AUC values (around 0.56 in METABRIC) suggest low discriminative potential, while the GEO validation cohort showed no meaningful survival separation.These findings should be evaluated more critically, and claims about clinical value should be limited correspondingly.
   4. ⁠Single-cell RNA-seq analysis is primarily descriptive. The scRNA-seq analysis provides important descriptive information, but it does not provide rigorous statistical testing of differential expression across cell types.Functional results of stromal and immunological involvement in ferroptosis regulation should be explicitly stated as exploratory.
   5. ⁠Biological Interpretation of AR and EZH2. AR and EZH2 are identified as important ferroptosis regulators; however, no mechanistic validation is offered. Several findings are based mainly on existing research rather than direct evidence from the presented data. The authors should use mild causal language and make it apparent that these findings generate hypotheses.
   6. ⁠Construction and validation of the Ferroptosis Index (FI) The FI relies on β-coefficients from the discovery cohort, which may lead to overfitting.The manuscript lacks internal validation (such as bootstrapping or cross-validation) and does not specify whether coefficients were recalibrated or fixed during external validation. Further explanation and a robustness check of the FI are required.
   7. ⁠Please include a paragraph outlining the limitations of this study 

Minor comments:
1. Create an organized schematic outlining the analytical workflow.
2. Determine the sample sizes for each analytical stage (particularly CPTAC and scRNA-seq).
3. Present effect size and confidence intervals consistently.
4. Improve figure readability (a few panels are too crowded).
5. ⁠Standardize terminology. (Basal-like and TNBC are used interchangeably).
6. ⁠Clearly state whether multiple testing correction was used in survival analyses.
7. ⁠Clarify the Methods for dataset access dates and versions.

Author Response

Reviewer 4

Responses to Reviewer 4

We sincerely thank the Reviewer for the thorough and critical evaluation of our manuscript and for the detailed, constructive comments. We appreciate the Reviewer’s careful attention to methodological rigor, interpretational clarity, and translational relevance. The comments significantly helped us to refine the conceptual framework of the study, clarify the limitations of our analyses, and more precisely define the biological and prognostic scope of our findings. All points raised by the Reviewer have been carefully addressed, as detailed below.

Major Comment 1. (Diagnostic versus Prognostic Claims The article contains multiple mentions to diagnostic relevance; nonetheless, the research findings (Cox regression, LASSO modeling, survival analysis, and FI stratification) suggest prognostic rather than diagnostic utility. There are no explicit diagnostic metrics available (such as classification ROC or sensitivity/specificity). The authors should make a clear distinction between diagnostic and prognostic statements, or modify the title and text accordingly.)

and

Major Comment 3. ⁠(The prognostic model has modest predictive performance. The presented AUC values (around 0.56 in METABRIC) suggest low discriminative potential, while the GEO validation cohort showed no meaningful survival separation. These findings should be evaluated more critically, and claims about clinical value should be limited correspondingly.)

Response:

We agree with the Reviewer that our analyses support prognostic rather than diagnostic utility and that the modest AUC values indicate limited predictive discrimination.  Accordingly, we revised the title and manuscript text to remove diagnostic claims and clearly distinguish prognostic interpretation. No diagnostic performance metrics were generated, and all claims have been limited accordingly.

To address this limitation transparently, we have revised the Discussion to explicitly state that the proposed gene signature and Ferroptosis Index should not be interpreted as independent clinical prognostic tools. Instead, they reflect ferroptosis-associated transcriptional states associated with overall survival and biological risk stratification. These changes have been introduced in the title of the manuscript, the Abstract Conclusion was revised (page 2, paragraph 1, lines 41-48), and Section 5. (Conclusion) was revised (page 28, paragraphs 6 and 7, lines 913-928). 

Specifically, in Section 3.2.2 (Construction and evaluation of ferroptosis-associated transcriptional stratification model- revised subtitle), we now explicitly state that the model demonstrates modest discriminatory performance and primarily captures biologically relevant differences in survival rather than providing definitive clinical prediction. These changes have been introduced on page 12, paragraph 2, lines 423-435, page 13, paragraph 3 and page 14, paragraph 1, lines 449-466.

In the Discussion, we further clarify that the model represents a ferroptosis-associated stratification framework reflecting transcriptional states linked to overall survival in Basal-like breast cancer, rather than an independent clinical predictor. These changes have been introduced on page 24, paragraph 2, lines 735-745, and page 25, paragraph 1, lines 746-748.

Also, we have revised Section 3.4 and Discussion to explicitly clarify that FI reflects a ferroptosis-associated transcriptional and metabolic stress state, representing the balance between pro- and anti-ferroptotic gene expression rather than execution of ferroptosis. We have expanded the Materials and Methods section to explicitly describe how FI was constructed, the origin of β-coefficients, and the intended interpretation of FI as a descriptive measure of ferroptosis-associated transcriptional potential rather than evidence of ongoing ferroptotic cell death. These clarifications have been added to page 7, paragraph 1, lines 246-253, page 16, Section 3.4. (Ferroptosis Index Analysis) paragraph 2, line 533; page 16, Section 3.4. (Ferroptosis Index Analysis) paragraph 3, line 541; and page 25, Section 4. (Discussion) paragraph 5, lines 790-793.

Major Comment 2. ⁠Lack of multivariable survival adjustment. Despite the presence of important clinicopathological factors (age, stage, grade, nodal status, and treatment), survival analyses are primarily conducted using univariate Cox regression. It's uncertain whether the hypothesized gene signature and the Ferroptosis Index are independent prognostic variables. Multivariable Cox models or a good explanation for their absence are required.

Response:
We thank the Reviewer for this important comment. We fully agree that multivariable survival modeling is essential when the goal is to establish independent clinical prognostic value. In the present study, however, our primary objective was not to develop a clinically deployable prognostic model, but rather to identify and characterize ferroptosis-associated transcriptional programs linked to survival and biological risk stratification within  Basal-like tumors.

Accordingly, univariate Cox regression was used to identify ferroptosis-related genes associated with overall survival, which were subsequently integrated into a biologically motivated ferroptosis-associated stratification framework.

Multivariable Cox adjustment for clinicopathological covariates (including age, stage, grade, nodal status, and treatment) was not performed due to substantial heterogeneity and incomplete harmonization of clinical annotations across the METABRIC, TCGA, and GEO cohorts. Performing multivariable modeling under these conditions could introduce bias or instability and would require rigorous cohort-specific harmonization beyond the scope of this study. Importantly, the absence of multivariable adjustment does not affect the primary conclusions of this work, which focus on biological signal discovery rather than clinical risk prediction.

To address this limitation transparently, we revised the Results and Discussion to clearly state that the proposed gene signature reflects ferroptosis-associated transcriptional states linked to survival trends, rather than independent clinical prognostic predictors. We further emphasize that future studies using harmonized, prospectively collected cohorts with standardized clinical annotation will be required to formally assess independence through multivariable modeling.

These clarifications have been added to Section 3.2.1 (Results) page 10, paragraph 3, lines 365–379, Section 4 (Discussion, Limitations paragraph) page 27, paragraph 6, lines 885–886, page 28, paragraph 1, lines 887–902.

Major Comment 4. Single-cell RNA-seq analysis is primarily descriptive. The scRNA-seq analysis provides important descriptive information, but it does not provide rigorous statistical testing of differential expression across cell types. Functional results of stromal and immunological involvement in ferroptosis regulation should be explicitly stated as exploratory.

Response:

We thank the Reviewer for this important observation. We fully agree that the single-cell RNA-seq analysis presented in this study is descriptive and does not include rigorous statistical testing of differential gene expression across cell types.

To address this concern, we have revised the Results and Discussion sections to explicitly state that the scRNA-seq findings are exploratory and hypothesis-generating. We now clearly emphasize that the observed expression of ferroptosis-related genes across cancer epithelial, stromal, and immune populations reflects potential cellular sources of ferroptosis-associated signals, rather than functional or causal regulation. Also, no formal statistical testing of differential expression across cell types was conducted due to the limited number of TNBC samples in the scRNA-seq dataset (n = 10).

Specifically, we added clarifying statements in the Results section (page 23, paragraph 3, lines 712-716), noting the descriptive nature of the scRNA-seq analysis, and in the Section 4 (Discussion, paragraph limitations) page 27, paragraph 6, lines 885–886, page 28, paragraph 1, lines 887–902, highlighting that stromal and immune involvement should be interpreted as exploratory and requires further functional validation. These revisions ensure appropriate interpretation of the single-cell data.

Major Comment 5. ⁠Biological Interpretation of AR and EZH2. AR and EZH2 are identified as important ferroptosis regulators; however, no mechanistic validation is offered. Several findings are based mainly on existing research rather than direct evidence from the presented data. The authors should use mild causal language and make it apparent that these findings generate hypotheses.

Response:
We thank the Reviewer for this important clarification. We fully agree that the present study does not provide direct mechanistic validation of AR or EZH2 in ferroptosis regulation. Accordingly, we have revised the Discussion to explicitly frame all interpretations regarding AR and EZH2 using mild, non-causal language and to clearly state that these findings are hypothesis-generating.

Specifically, we now emphasize that while AR downregulation and EZH2 upregulation are established hallmarks of Basal-like biology, the novelty of our study lies in positioning these factors within a ferroptosis-associated regulatory context based on integrative transcriptomic, proteomic, and survival analyses. We explicitly state that proposed links between AR, EZH2, redox balance, lipid metabolism, and ferroptosis susceptibility are inferred from integrated omics patterns and supported by prior literature, rather than demonstrated by direct functional experiments within this study.

These revisions have been introduced in Section 4 (Discussion), page 27, paragraph 3, lines 866-874, where we clearly describe the AR/EZH2 findings as exploratory and hypothesis-generating.

 Major Comment 6. ⁠Construction and validation of the Ferroptosis Index (FI) The FI relies on β-coefficients from the discovery cohort, which may lead to overfitting. The manuscript lacks internal validation (such as bootstrapping or cross-validation) and does not specify whether coefficients were recalibrated or fixed during external validation. Further explanation and a robustness check of the FI are required.

 Response:
We thank the Reviewer for this important methodological comment. We agree that when an index is intended for prediction, internal validation and robustness assessment are essential. In the present study, however, the Ferroptosis Index (FI) was not designed as a predictive or prognostic classifier, but as a descriptive, biology-oriented measure summarizing ferroptosis-associated transcriptional states.

To address this transparently, we have revised the Methods and Discussion to clearly state that FI β-coefficients were derived exclusively from the METABRIC Basal-like cohort and were not recalibrated, retrained, or externally validated as a predictive score. The FI was calculated solely within the METABRIC cohort to assess relative enrichment of ferroptosis-associated transcriptional programs across intrinsic subtypes, rather than to estimate survival risk.

Because FI was not intended as a predictive model, internal validation procedures such as bootstrapping or cross-validation were not performed, as they would not be methodologically appropriate for a descriptive index. We explicitly clarify that FI does not imply ongoing ferroptotic cell death, nor does it represent an independent clinical prognostic tool but rather reflects a ferroptosis-poised transcriptional and metabolic stress state.

These clarifications have been added to page 7, paragraph 1, lines 246-253, page 16, Section 3.4. (Ferroptosis Index Analysis) paragraph 2, line 533; page 16, Section 3.4. (Ferroptosis Index Analysis) paragraph 3, line 541; and page 25, Section 4. (Discussion) paragraph 5, lines 790-793, where we now clearly delineate the biological scope and limitations of the FI.

Major Comment 7. Please include a paragraph outlining the limitations of this study

Response:
We thank the Reviewer for this important suggestion. A dedicated paragraph outlining the limitations of the study has now been added to the Discussion section. In this paragraph, we explicitly address the retrospective nature of the analyzed datasets, the lack of functional validation for key regulators, limitations related to model construction and validation, the use of primarily univariate survival analyses, cohort heterogeneity, and the descriptive nature of the single-cell RNA-seq analysis. These limitations and future directions are now clearly articulated to ensure transparent interpretation of the findings.

This paragraph has been added to Section 4 (Discussion), page 27, paragraph 6, lines 885–886, page 28, paragraph 1, lines 887–902in the revised manuscript.

Minor Comment 1. Create an organized schematic outlining the analytical workflow

Response:

We thank the Reviewer for this suggestion. We clarified the relationship between survival-associated genes, FI construction, and scRNA-seq analysis in the workflow schematic (Figure 1).

Minor Comment 2. Determine the sample sizes for each analytical stage (particularly CPTAC and scRNA-seq).

Response:

We thank the Reviewer for this suggestion. We have now explicitly reported sample sizes for each analytical stage in the Methods section. Sample sizes across analytical stages were as follows: the METABRIC Basal-like/TNBC cohort (n = 209) was used as the discovery dataset, with baseline clinical characteristics summarized in Supplementary Table S1. The CPTAC proteomics cohort included a total of 124 samples (Basal-like n = 29, Luminal A n = 57, Luminal B n = 17, HER2-enriched n = 16, Normal-like n = 5). TCGA and GEO cohorts were used for external validation and included TCGA n=1081 and GEO n=104 samples. Single-cell RNA-seq analysis (GSE176078) comprised tumor samples from 10 TNBC patients. These clarifications have been added to the revised manuscript. This paragraph has been added to Section 2 (Materials and Methods), page 4, paragraph 4, lines 152-157.

Minor Comment 3. Present effect size and confidence intervals consistently.

Response:

We thank the Reviewer for this comment. Effect sizes and 95% confidence intervals are now consistently reported for survival analyses. This has now been explicitly stated in the Results section (Section 3.2.1), page 10, paragraph 3, lines 376-378 and clarified in the Methods. LASSO-derived β-coefficients were used for score construction only and are not interpreted as inferential effect sizes with confidence intervals, in the Section 2. (Materials and Methods, LASSO regularization for Cox regression), page 6, paragraph 1, lines 212-214. Kaplan–Meier analyses were compared using the log-rank test, Section 2. (Materials and Methods, Kaplan-Meier analysis), page 6, paragraph 2, lines 216-220.  In the Section 3. (Resluts, 3.5.5. Survival analysis of ferroptosis-related gene expression in the METABRIC cohort) hazard ratios with corresponding 95% confidence intervals derived from univariate Cox regression are provided on, page 20, paragraph 3, lines 642-651.

Minor Comment 4. Improve figure readability (a few panels are too crowded).

Response:

We thank the reviewer for pointing out this issue. The overwritten pathway names in Figure S5C and 5D have been resolved.

 

Minor Comment 5. Standardize terminology. (Basal-like and TNBC are used interchangeably).

Response:

We thank the Reviewer for pointing out the inconsistent use of the terms Basal-like and TNBC. We have corrected this throughout the manuscript. All molecular analyses and results are now reported exclusively using the Basal-like subtype, which represents a molecular classification rather than a diagnostic entity. The term TNBC is used only in the Introduction and Discussion to provide clinical context, acknowledging that while most TNBCs exhibit a Basal-like transcriptional profile, these terms are not interchangeable. This clarification has been implemented consistently across the revised manuscript.

Minor Comment 6. ⁠Clearly state whether multiple testing correction was used in survival analyses.

Response:

We thank the Reviewer for this important comment. We have now explicitly clarified in the Methods section that multiple-testing correction was not applied to the gene-level survival analyses. This decision reflects the hypothesis-driven design of the study and the restriction of analyses to a predefined, biologically curated set of ferroptosis-related genes, rather than a genome-wide screening. Accordingly, p-values are reported as nominal and interpreted in a biological and exploratory context. These changes have been introduced in Section 2 (Material and Methods), page 7, paragraph 2, lines 264-268.

 Minor Comment 7. ⁠Clarify the Methods for dataset access dates and versions.

Response:

We thank the Reviewer for this comment. We have revised the Methods section to clearly specify the data sources, access dates, and data retrieval tools for all datasets used in this study. The access dates for METABRIC, TCGA, GEO, CPTAC, and the scRNA-seq dataset (GSE176078) are now explicitly stated. We also clarified that data were retrieved using the cBioPortalData R package and public repository-specific access tools, ensuring transparency and reproducibility. These changes have been introduced in Section 2 (Material and Methods), page 5, paragraph 4, lines 182-183 and page 7, paragraph 2, lines 267-368.

Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

Authors revised manuscript.

Reviewer 3 Report

Comments and Suggestions for Authors

Thanks for addressing all the comments and improving the manuscript.

Reviewer 4 Report

Comments and Suggestions for Authors

All reviewer concerns have been satisfactorily addressed. The manuscript has been appropriately revised, with corrected claims and clearly stated limitations.