A Conserved Fibroblast-Myeloid Gene Signature in Digestive Cancers: Multi-Omics Integration Identifies DCN, COL10A1, CTHRC1, and TREM2 as Candidate Microenvironmental Markers

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The work entitled "A Conserved Core Signature of the Tumor Microenvironment in Digestive Cancers: Integrated Multi-Omics Analysis Identifies DCN, COL10A1, CTHRC1 and 3 TREM2 as Key Regulators" shows interesting information but requires experimental confirmation.

• I believe that the work is merely predictive and would need experimental confirmation, even if only of some identified genes.
• It is necessary to add the identification codes of the datasets collected in the UCSC Xena database.
• Ithenticate shows a 7% similarity to another manuscript and highlights an attempt to make it harder to detect similarities by replacing characters with similar-looking ones from different alphabets or character sets.
• In the discussion, the authors should mention what role each of the identified genes (DCN, COL10A1, CTHRC1 and TREM2) might play in gastrointestinal cancers.
• What is the clinical value of your observations?

Author Response

Thank you very much for taking the time to review this manuscript. Please find the detailed responses below. The revised portions of the manuscript have been highlighted in red.

Comments 1: The work entitled "A Conserved Core Signature of the Tumor Microenvironment in Digestive Cancers: Integrated Multi-Omics Analysis Identifies DCN, COL10A1, CTHRC1 and 3 TREM2 as Key Regulators" shows interesting information but requires experimental confirmation.
I believe that the work is merely predictive and would need experimental confirmation, even if only of some identified genes.
Response 1:Thank you very much for your valuable suggestion. We fully agree that additional experimental validation would be highly necessary. However, due to limitations in resources and time, we are currently unable to perform the corresponding experiments, for which we sincerely apologize.
Nevertheless, our multi-omics bioinformatics analyses provide consistent support for our hypothesis that digestive cancers may share a common molecular mechanism. In addition, we have expanded our analysis by incorporating cell–cell communication results, which further reveal consistent signaling pathways across digestive cancers. Based on these findings, we propose a potential mechanistic model, which is described in detail in Section 2.6 of the revised manuscript.

Comments 2: It is necessary to add the identification codes of the datasets collected in the UCSC Xena database.
Response 2: Thank you very much for your valuable suggestion. We apologize for this oversight on our part. The corresponding dataset IDs have now been added in Sections 4.1 and 4.11 of the revised manuscript.

Comments 3: Ithenticate shows a 7% similarity to another manuscript and highlights an attempt to make it harder to detect similarities by replacing characters with similar-looking ones from different alphabets or character sets.
Response 3: We take this concern very seriously and would like to clarify the matter explicitly. We assure you that this manuscript does not involve plagiarism of any published work, nor does it employ character substitution or any other means to evade similarity detection. The reported 7% similarity may arise from several factors.
First, many bioinformatics analysis pipelines are highly standardized. For example, in single-cell RNA sequencing analysis, it is routine to perform preprocessing steps to filter low-quality cells, followed by normalization, batch effect correction, and finally cell type annotation. These standard workflows are commonly used across studies, which can naturally lead to some degree of textual similarity with other publications.
Second, this manuscript contains numerous domain-specific technical terms, such as epithelial–mesenchymal transition and extracellular matrix. The frequent use of such standardized terminology can also contribute to overlap with other works.
Finally, our bioinformatics analyses rely on several widely used R packages, and the corresponding citations have been included accordingly. Since these tools are commonly adopted in the field, the referenced literature may overlap with that of other studies.
Taken together, these factors may explain the observed similarity, particularly in the context of bioinformatics-related manuscripts.

Comments 4: In the discussion, the authors should mention what role each of the identified genes (DCN, COL10A1, CTHRC1 and TREM2) might play in gastrointestinal cancers.
Response 4: Thank you very much for your valuable suggestion, which is highly important for a better understanding of the content of this manuscript. After incorporating the cell–cell communication analysis, we have gained deeper insights into the conserved signaling pathways across digestive cancers. We will reflect and further elaborate on this aspect in the Discussion section of the revised manuscript.

Comments 5: What is the clinical value of your observations?
Response 5: Thank you very much for your question. The clinical significance of our study can be summarized in the following aspects. First, the logistic regression model constructed using the four genes demonstrates good performance and may assist in the clinical diagnosis of digestive cancers. Second, the high- and low-expression groups of the four genes (DCN, CTHRC1, COL10A1, and TREM2) show significant differences in overall survival, suggesting their potential utility in patient prognosis evaluation. Finally, the expression levels of these four genes are significantly correlated with the IC50 values of multiple drugs, indicating their potential value in guiding therapeutic strategies.

Reviewer 2 Report

Comments and Suggestions for Authors

This study is part of a broad trend in bioinformatics known as “pan-cancer” analysis of public data, addressing the epidemiologically significant topic of gastrointestinal cancers. The authors identify four genes (DCN, COL10A1, CTHRC1, TREM2) as common regulators of the TME across seven cancer types. While the hypothesis is not without biological merit, the execution raises serious methodological concerns: the study is entirely computational, relies solely on public data, and the key diagnostic model exhibits characteristics typical of overfitting or a technical artifact. The central question of the study (“Is there a conserved core of the TME in gastrointestinal cancers?”) is valid, but the answer proposed by the authors largely confirms what is already known. DCN as a tumor suppressor and a component of the ECM, CTHRC1 as a promoter of invasion via the WNT/PCP pathway, COL10A1 in fibroblasts, TREM2 in immunosuppressive macrophages—all four genes have a well-established body of literature in oncology. The authors do not indicate what specifically new their work contributes beyond replicating known observations on a new dataset. There is no clear “gap in knowledge” that this work is intended to fill.

The comparison of TCGA and GTEx as “tumor vs. normal” is the most serious methodological criticism of the entire study. The diagnostic model (AUC > 0.98) is built on TCGA (tumor) vs. GTEx (healthy tissue from non-cancer patients) data. These are two separate sequencing projects—different RNA extraction protocols, different libraries, different sequencing centers, and different sample storage times. Logistic regression on such data does not distinguish cancerous tissue from normal tissue—it learns the batch effect between TCGA and GTEx. An AUC > 0.98 is then not evidence of the biomarker’s diagnostic value, but evidence of the batch classifier’s effectiveness. This is a well-known problem in the literature (see Wang et al., 2019, Brief. Bioinform.). The authors do not discuss this at all. This is a flaw that disqualifies Section 2.6 as a whole in its current form.

Another issue is that the entire pipeline is run on the same TCGA data:

• DEGs identified from TCGA → WGCNA applied to these DEGs → Cox/LASSO/RF applied to the same samples → diagnostic model built and validated on a subset of the same samples.

A 70/30 split on a homogeneous TCGA+GTEx dataset is not external validation — it is internal validation on data that participated (indirectly) in gene selection. There is not a single independent validation cohort from another center or platform. In such a design, AUC inflation is inevitable.

Typically, WGCNA is performed on the entire transcriptome or a large portion of it, and then modules are identified. Here, WGCNA is fed a set of 540 genes that have already been selected as “common DEGs across 7 cancer types.” This radically narrows the search space and artificially strengthens correlations within the clusters (genes selected as differentially expressed inherently have high variance, which WGCNA favors). Such a design leads to clusters that are “doomed” to functional coherence even before the analysis is performed.

The Kaplan-Meier curves are stratified according to the “optimal cutoff” for the GSVA score (Section 2.2). Selecting the cutoff post-hoc using the same data that is later used for the log-rank test significantly affects the p-value. The authors do not apply any correction (e.g., Contal-O'Quigley, permutation test). All p-values reported from these analyses are overestimated by an unknown amount.

The multivariate analysis (Section 2.3) is performed on pooled samples from 7 tumor types—but tumor type is omitted as a variable in the model. This is a fundamental error: the strongest predictor of prognosis in this dataset is tumor type (PAAD has a dramatically worse prognosis than READ). Omitting this confounder means that the “independent prognostic factors” are in fact markers of tumor types with different prognoses, rather than prognostic variables within the types. The intersection of the results from the four methods (univariate Cox, multivariate Cox, LASSO, RF) is presented as a rigorous and objective approach. In reality, this is arbitrary—the choice of thresholds (p < 0.05 for Cox, lambda.1se for LASSO, top 15 for RF) is neither justified nor sensitivity-tested. Changing the lambda threshold in LASSO or the number of top genes from RF could yield a completely different set of genes. No sensitivity analysis.

Drug sensitivity analysis is based on the correlation between gene expression in TCGA samples (in vivo, complex tissue) and IC50 values in cell lines (in vitro, monoculture). This approach is widely used, but its interpretation is severely limited: DCN expression in tumor fibroblasts does not directly indicate how cancer cells (and only cancer cells) will respond to the drug. The authors present these correlations as “valuable clues for personalized therapy”—this is an overinterpretation.

The results section contains also the following inconsistencies and omissions:

• No sample sizes for the diagnostic model. How many samples are in the training/test sets?
• What is the tumor-to-normal ratio? Without this information, the AUC assessment is incomplete.
• No 95% CI for AUC — a standard requirement for reporting ROC results.
• COL10A1 absent from the alternative splicing analysis — Section 2.5 describes AS data for DCN, CTHRC1, and TREM2, completely omitting COL10A1 without any explanation. This is an internal inconsistency in the article.
• Figure 1 (flowchart) takes up the entire page 3 — typical “padding” with no analytical value.
• The GS vs. MM correlations in the yellow module (Fig. 2C-K) are presented as evidence of “strong internal connectivity”—but this is an expected property of every WGCNA module and provides no additional information beyond the fact that the module was correctly identified.

The discussion is largely a review of the literature combined with the results, without any in-depth mechanistic analysis. The authors correctly list the limitations (lack of experimental validation, unclear mechanisms), but fail to mention the most serious limitation—the issue of the TCGA/GTEx batch effect as a confounder in the diagnostic model. The statement “CTHRC1 alone exhibited the best diagnostic performance, with an AUC exceeding 0.9” is made without any qualification regarding the technical artifact.

Author Response

Thank you for taking the time to review our manuscript and for providing insightful and constructive comments. Your feedback has been highly valuable in helping us improve the quality of our work. Below, we provide point-by-point responses to each of your comments, and the corresponding revisions have been highlighted in the resubmitted manuscript.

Comments 1: This study is part of a broad trend in bioinformatics known as “pan-cancer” analysis of public data, addressing the epidemiologically significant topic of gastrointestinal cancers. The authors identify four genes (DCN, COL10A1, CTHRC1, TREM2) as common regulators of the TME across seven cancer types. While the hypothesis is not without biological merit, the execution raises serious methodological concerns: the study is entirely computational, relies solely on public data, and the key diagnostic model exhibits characteristics typical of overfitting or a technical artifact. The central question of the study (“Is there a conserved core of the TME in gastrointestinal cancers?”) is valid, but the answer proposed by the authors largely confirms what is already known. DCN as a tumor suppressor and a component of the ECM, CTHRC1 as a promoter of invasion via the WNT/PCP pathway, COL10A1 in fibroblasts, TREM2 in immunosuppressive macrophages—all four genes have a well-established body of literature in oncology. The authors do not indicate what specifically new their work contributes beyond replicating known observations on a new dataset. There is no clear “gap in knowledge” that this work is intended to fill.
Response 1:Thank you very much for your valuable and precise comments. We acknowledge that our study has certain limitations, as all analyses were conducted based on publicly available bioinformatics datasets. These limitations will be discussed in the Discussion section of the revised manuscript.
Regarding the model construction, we have reanalyzed the data. Specifically, we used the TCGA dataset for model development and the GEO dataset for external validation. The detailed procedures are provided in Section 2.7 of the manuscript.
As you pointed out, these four genes have indeed been studied previously; however, most prior studies have focused on the role of individual genes in a specific cancer type. In contrast, our study aims to investigate the shared characteristics of these genes across digestive cancers.
Specifically, the value of our study is reflected in several aspects. First, through single-cell analysis, we localized the expression of these four genes and revealed their consistent expression patterns across multiple digestive cancers. In particular, DCN, CTHRC1, and COL10A1 are predominantly expressed in mCAFs, while TREM2 is mainly expressed in myeloid cells, with a smaller fraction detected in apCAFs. Second, through immune infiltration analysis, pathway correlation analysis, and enrichment analysis, we demonstrated that these genes exhibit similar functional associations across multiple cancers, potentially involving extracellular matrix remodeling and epithelial–mesenchymal transition processes.
In addition, cell–cell communication analysis revealed that multiple ligand–receptor interactions are consistently present across digestive cancers. Based on these findings, we propose a previously undescribed conserved stromal-associated signature, although this remains a hypothesis at this stage. Finally, survival analyses and the constructed model suggest that these genes may have potential value in the diagnosis and prognosis of digestive cancers.

Comments 2: The comparison of TCGA and GTEx as “tumor vs. normal” is the most serious methodological criticism of the entire study. The diagnostic model (AUC > 0.98) is built on TCGA (tumor) vs. GTEx (healthy tissue from non-cancer patients) data. These are two separate sequencing projects—different RNA extraction protocols, different libraries, different sequencing centers, and different sample storage times. Logistic regression on such data does not distinguish cancerous tissue from normal tissue—it learns the batch effect between TCGA and GTEx. An AUC > 0.98 is then not evidence of the biomarker’s diagnostic value, but evidence of the batch classifier’s effectiveness. This is a well-known problem in the literature (see Wang et al., 2019, Brief. Bioinform.). The authors do not discuss this at all. This is a flaw that disqualifies Section 2.6 as a whole in its current form.
Response 2: Thank you for pointing this out. We fully agree with your concern. In response, we have thoroughly revised the model construction section. Specifically, we now use the TCGA dataset as the training set and the GEO dataset for external validation.
Given the substantial imbalance between tumor and normal samples in the TCGA dataset, we applied both undersampling and oversampling techniques to balance the training data and avoid model bias. However, the validation set still suffers from a limited number of normal samples. This limitation will be explicitly acknowledged and discussed in the Discussion section of the revised manuscript.

Comments 3: Another issue is that the entire pipeline is run on the same TCGA data:
DEGs identified from TCGA → WGCNA applied to these DEGs → Cox/LASSO/RF applied to the same samples → diagnostic model built and validated on a subset of the same samples.
Response 3: Thank you for pointing this out. We fully understand your concern that performing multiple rounds of feature selection on the same dataset may introduce a risk of overfitting. After revising the model, its performance remains robust, with an AUC of 0.925 (95% CI: 0.824–1.000) in the validation set.
In addition, other parts of our study, such as the single-cell analysis, were conducted on independent datasets that were not involved in the initial feature selection. Notably, these analyses also yielded consistent and concordant results, further supporting the robustness of our findings.

Comments 4: A 70/30 split on a homogeneous TCGA+GTEx dataset is not external validation — it is internal validation on data that participated (indirectly) in gene selection. There is not a single independent validation cohort from another center or platform. In such a design, AUC inflation is inevitable.
Response 4: Thank you for raising this issue. We have thoroughly revised this part of the study. Specifically, we constructed the model using the TCGA dataset and performed external validation on the GEO dataset (GSE39582). The AUC values of the ROC curves for the training and validation sets are 0.958 (95% CI: 0.942–0.975) and 0.925 (95% CI: 0.824–1.000), respectively.
The detailed revisions can be found in Sections 2.7 and 4.11, as well as in Figure 11 of the revised manuscript.

Comments 5: Typically, WGCNA is performed on the entire transcriptome or a large portion of it, and then modules are identified. Here, WGCNA is fed a set of 540 genes that have already been selected as “common DEGs across 7 cancer types.” This radically narrows the search space and artificially strengthens correlations within the clusters (genes selected as differentially expressed inherently have high variance, which WGCNA favors). Such a design leads to clusters that are “doomed” to functional coherence even before the analysis is performed.
Response 5: Thank you for raising this question. Our initial intention in performing differential expression analysis followed by intersection was to narrow down the candidate gene set. However, we acknowledge that this approach may lead to the omission of some key genes and potentially important modules, meaning that the identified genes may not represent all biologically significant factors. Our primary objective was to identify key shared genes and underlying mechanisms across digestive cancers, rather than to exhaustively capture all common features.

Comments 6: The Kaplan-Meier curves are stratified according to the “optimal cutoff” for the GSVA score (Section 2.2). Selecting the cutoff post-hoc using the same data that is later used for the log-rank test significantly affects the p-value. The authors do not apply any correction (e.g., Contal-O'Quigley, permutation test). All p-values reported from these analyses are overestimated by an unknown amount.
Response 6: Thank you for raising this important statistical concern. We agree that using an “optimal cutoff value” derived from the same dataset for survival analysis may introduce bias and lead to underestimated P values .
To address this issue, we have revised the statistical approach for the survival analysis. In the revised manuscript, we applied a permutation test to evaluate the significance of the optimal cutoff values used in the survival analyses presented in Figures 2D–G. We have explicitly indicated in the updated figure legends that permutation testing was applied, and we have also added a corresponding description in Section 4.3 of the revised manuscript.

Comments 7: The multivariate analysis (Section 2.3) is performed on pooled samples from 7 tumor types—but tumor type is omitted as a variable in the model. This is a fundamental error: the strongest predictor of prognosis in this dataset is tumor type (PAAD has a dramatically worse prognosis than READ). Omitting this confounder means that the “independent prognostic factors” are in fact markers of tumor types with different prognoses, rather than prognostic variables within the types. The intersection of the results from the four methods (univariate Cox, multivariate Cox, LASSO, RF) is presented as a rigorous and objective approach. In reality, this is arbitrary—the choice of thresholds (p < 0.05 for Cox, lambda.1se for LASSO, top 15 for RF) is neither justified nor sensitivity-tested. Changing the lambda threshold in LASSO or the number of top genes from RF could yield a completely different set of genes. No sensitivity analysis.
Response 7: Thank you for raising this important question and concern. We acknowledge that only genes were included as variables in the multivariate regression analysis, which was done intentionally. Our objective was to identify shared key genes and underlying molecular mechanisms across digestive cancers. Therefore, we removed cancer-type labels and treated all digestive cancers as a single cohort, as prognostic differences among cancers are largely influenced by gene-level factors.
In this context, analyzing all digestive cancers collectively helps avoid artificially introducing categorical labels. Moreover, within existing cancer classifications, further subtyping is possible (e.g., colon cancer can be subdivided into ascending, transverse, descending, and sigmoid colon cancers). However, such additional stratification is not commonly applied in similar analyses, where cancers are often treated as broader categories without further artificial subdivision.
That said, we agree that under this analytical framework, the selected genes should not strictly be referred to as independent prognostic genes, and we have revised the relevant descriptions in Section 2.3 accordingly. In addition, we generated KM survival curves for these four genes across all digestive cancers and performed permutation tests; the results are presented in Supplementary Figure S2.
Regarding the LASSO regression and Random Forest analyses, we acknowledge that the selection of the lambda parameter and the choice of the top 15 genes involve a certain degree of subjectivity. This limitation has now been explicitly discussed in the Discussion section. Furthermore, in the logistic regression model, we conducted variance inflation factor (VIF) analysis, and all four genes showed VIF values below 5, indicating no significant multicollinearity (see Figure S11E). Although these four genes may not represent the most central or dominant drivers, they do exhibit a certain degree of shared relevance across digestive cancers.

Comments 8: Drug sensitivity analysis is based on the correlation between gene expression in TCGA samples (in vivo, complex tissue) and IC50 values in cell lines (in vitro, monoculture). This approach is widely used, but its interpretation is severely limited: DCN expression in tumor fibroblasts does not directly indicate how cancer cells (and only cancer cells) will respond to the drug. The authors present these correlations as “valuable clues for personalized therapy”—this is an overinterpretation.
Response 8: Thank you for pointing this out. We agree that directly correlating gene expression derived from complex tissues with drug sensitivity data obtained from in vitro cell lines has inherent limitations in interpretation, particularly when the genes are predominantly expressed in stromal cells. We have accordingly tempered the interpretation of these results in Section 2.7 and in the Discussion section of the revised manuscript.

Comments 9: The results section contains also the following inconsistencies and omissions:
No sample sizes for the diagnostic model. 
How many samples are in the training/test sets?
What is the tumor-to-normal ratio? 
Without this information, the AUC assessment is incomplete.
No 95% CI for AUC — a standard requirement for reporting ROC results.
Response 9: Thank you for pointing out the missing key information. As described in our responses to Comments 2 and 4, we have thoroughly revised the diagnostic model section and have fully incorporated all the information you requested in the revised manuscript. Specifically, we have clearly reported the sample sizes of the training and validation sets in Section 4.11. In the updated Figures 11C and 11D, we provide the AUC values along with their corresponding 95% confidence intervals for each ROC curve, and these details have also been consistently updated in Section 2.7.

Comments 10: COL10A1 absent from the alternative splicing analysis — Section 2.5 describes AS data for DCN, CTHRC1, and TREM2, completely omitting COL10A1 without any explanation. This is an internal inconsistency in the article.
Response 10: Thank you for pointing out this oversight. We did not analyze the alternative splicing of COL10A1 because reliable alternative splicing event data for COL10A1 is not available in the OncoSplicing database. To avoid any potential confusion for readers, we have added an appropriate explanation in Section 4.8 and in the legend of Figure 9 in the revised manuscript.

Comments 11: Figure 1 (flowchart) takes up the entire page 3 — typical “padding” with no analytical value.
Response 11: Thank you for your suggestion. In the revised manuscript, we have removed Figure 1(flowchart).

Comments 12: The GS vs. MM correlations in the yellow module (Fig. 2C-K) are presented as evidence of “strong internal connectivity”—but this is an expected property of every WGCNA module and provides no additional information beyond the fact that the module was correctly identified.
Response 12: Thank you for your insightful comment. We agree that the high correlation between GS and MM is an inherent property of WGCNA-defined modules. In the original manuscript, we may have overemphasized this point. To streamline the content and highlight more meaningful findings, we have revised the description in Section 2.1 and removed statements that may have led to overinterpretation.
Subsequent analyses, including enrichment analysis, pathway correlation analysis, and single-cell analysis, further support that the genes within the identified modules exhibit strong intrinsic associations.

Comments 13: The discussion is largely a review of the literature combined with the results, without any in-depth mechanistic analysis. The authors correctly list the limitations (lack of experimental validation, unclear mechanisms), but fail to mention the most serious limitation—the issue of the TCGA/GTEx batch effect as a confounder in the diagnostic model. The statement “CTHRC1 alone exhibited the best diagnostic performance, with an AUC exceeding 0.9” is made without any qualification regarding the technical artifact.
Response 13: Thank you for pointing out these limitations. In response to your comments, we have made substantial revisions to the manuscript as follows:
First, the model section has been completely revised. However, the issue of a limited number of normal samples in the validation set still remains. We have explicitly acknowledged this limitation in the Discussion section.
Second, we have removed overgeneralized statements such as “CTHRC1 alone shows the best diagnostic performance with an AUC exceeding 0.9.” In the revised Section 2.7, we now cautiously report the diagnostic performance of both the single-gene and four-gene models based on the updated analysis, and we emphasize that the multi-gene model demonstrates superior performance. The limitations of this approach are also discussed.
Third, we have strengthened the mechanistic interpretation. In particular, we further elaborate on the fibroblast–myeloid cell communication axis (ECM–CD44) revealed by the single-cell analysis, and discuss in more depth how this axis may contribute to tumor progression and immune suppression. This revision aims to go beyond a literature summary and instead integrate our findings into an existing mechanistic framework.

Reviewer 3 Report

Comments and Suggestions for Authors

The manuscript addresses an important and potentially interesting question, namely whether a conserved tumor-microenvironment program can be identified across multiple digestive cancers. The attempt to integrate bulk transcriptomics, WGCNA, scRNA-seq, mutation, methylation, splicing, immune correlation, drug sensitivity, and diagnostic modeling is ambitious, and the identification of a stromal/myeloid-centered signature is not in itself implausible. The main signal the study recovers, especially around ECM remodeling, fibroblast biology, and TREM2-associated myeloid biology, is biologically coherent. However, in its current form the work is considerably more descriptive than mechanistic, and several core analytical choices are not sufficiently rigorous to support the strength of the claims being made. In particular, the manuscript repeatedly moves from correlation to causation, and from pan-cancer association to translational promise, without the level of validation that would be needed for such conclusions.

My main concern is that the study design is heavily predisposed to rediscover a broad stromal/mesenchymal signal rather than a truly conserved regulatory program specific to digestive cancers. The authors begin by intersecting differential expression results across seven tumor types and then apply WGCNA to the shared 540 protein-coding genes, ultimately focusing on a 32-gene module enriched for ECM-related functions and strongly linked to stromal indices. Given that the input genes are already restricted to those consistently dysregulated across very different tissues, and given that tumor-versus-normal comparisons were built from TCGA plus GTEx data, it is not surprising that the dominant output is a fibroblast/ECM signature. In other words, the pipeline seems optimized to capture common stromal admixture rather than tumor-intrinsic conserved biology. This is especially important because the paper later interprets DCN, COL10A1, CTHRC1, and TREM2 as “key regulators,” whereas the data presented mainly show that these genes mark matrix CAF or myeloid abundance and correlate with stromal programs. The evidence provided does not establish regulatory hierarchy, only repeated association with known microenvironmental states.

A second major issue is the insufficient handling of confounding and model inflation in the clinical and diagnostic sections. The prognostic screening combines univariate Cox, multivariate Cox, LASSO, and random forest, and then takes the intersection to define four hub genes. That sounds rigorous on paper, but the manuscript does not clearly describe how covariates were handled across cancers, whether proportional hazards assumptions were checked, whether multicollinearity among ECM genes was assessed, or whether the multivariable model included standard clinicopathologic factors beyond survival endpoints and stage correlations. The same problem becomes even more serious in the diagnostic section. The logistic model is built and tested by random 70/30 splitting of the same TCGA+GTEx-derived matrix, and the manuscript highlights AUC values above 0.98 with sensitivity and specificity above 0.95. Without an external validation cohort, this is not convincing evidence of clinical utility; it is much more likely to reflect dataset-specific separation, tissue composition differences, and TCGA-versus-GTEx batch structure. The fact that the authors use TCGA and GTEx together for tumor-normal discrimination, yet do not present a strategy for harmonization beyond using Xena TPM values, is a serious weakness. A model trained under those conditions can easily learn platform and tissue-source differences rather than disease biology.

Related to this, the manuscript’s own supplementary data undermine some of the confidence of the translational claims. The text states that CTHRC1 alone shows AUC > 0.9 across all digestive cancers, but the supplementary ROC plots for the other genes show that performance is quite variable depending on the gene and cancer type, with clearly weak performance in some cohorts, for example COL10A1 in LIHC and STAD and combined analyses that are far less impressive than the main model narrative suggests. Likewise, the manuscript presents the four-gene model as broadly robust, but robustness is not the same thing as an internal split of one pooled dataset. The same caution applies to the drug-sensitivity section, where correlations with CTRP and GDSC IC50 values are presented as therapeutically suggestive. These are only expression–drug correlations from cell-line based resources accessed through GSCA, not functional validation, not tumor-context testing, and certainly not evidence for drug repurposing or patient stratification. Those claims should be toned down substantially.

The single-cell part is probably the strongest section conceptually, but it still needs tighter analysis and more careful language. The authors assembled six GEO scRNA-seq datasets covering six digestive cancers and conclude that DCN, COL10A1, and CTHRC1 are enriched in mCAFs while TREM2 is enriched in myeloid cells and at lower levels in apCAFs. That general pattern is believable and consistent with current biology. Still, the manuscript overstates what the presented analyses can support. The statement that consistent cell composition across samples indicates the phenomenon is “not due to batch effects” is not justified; similar composition does not exclude residual technical or dataset-driven bias. More importantly, the cell annotation framework is not described with enough depth to evaluate whether mCAF and apCAF assignments are robust across all six datasets, especially because these datasets differ in platform, disease context, sample quality, and depth. The use of Harmony, DoubletFinder, and canonical markers is fine as a starting point, but it is not a substitute for showing integrated quality metrics, batch mixing diagnostics, cluster stability, or dataset-wise reproducibility of the key expression patterns. In addition, the manuscript jumps from cell-type localization to functional claims about EMT, antigen presentation, and immune modulation without direct cell-cell communication, trajectory, regulon, or perturbation analyses. As written, the scRNA-seq results support cell-of-origin mapping of the signature, but not the stronger mechanistic model the discussion advances.

The multi-omics sections also need to be interpreted more cautiously. The SNV, CNV, methylation, alternative splicing, pathway-correlation, and immune-correlation analyses are presented one after another, but most remain associative overlays on the same four genes. For example, SNVs are reported to have little survival impact except in esophageal carcinoma, CNVs are said to influence survival, CTHRC1 methylation is negatively correlated with expression, and DCN splicing has opposite prognostic implications across tumor types. Rather than reinforcing a unified model, these results often point to context dependence and heterogeneity. Yet the discussion smooths over that heterogeneity and presents the four genes as conserved regulators with strong diagnostic, prognostic, and therapeutic potential. That conclusion is stronger than the data justify. A more accurate interpretation would be that the study identifies a recurrent stromal/myeloid-associated signature across digestive tumors, composed of genes with known relevance to ECM and immune biology, and that these genes deserve follow-up validation. That would still be useful, but it is a narrower and more defensible claim than the current framing.

There are also multiple presentation and writing issues that need attention before publication. The manuscript contains a number of grammatical problems and overstatements, and some terminology is imprecise. For example, the methods section states that the “soft-power threshold was set to 0.9,” while the results and figure legend refer to a soft-thresholding power of 12, which is contradictory and needs correction. Figure labeling is occasionally awkward, and the writing repeatedly uses causal phrases such as “orchestrate tumor progression” or “key regulators” when only correlative evidence is shown. The abbreviation section and data availability statement are helpful, but the reproducibility standard is still not sufficient because the paper does not provide code, parameter settings in enough detail, or a transparent external validation workflow. If this manuscript is to be considered further, the authors should at minimum reframe the study more conservatively, correct methodological inconsistencies, provide stronger details for preprocessing and modeling, perform validation in truly independent cohorts, and avoid claiming diagnostic or therapeutic readiness from internal bioinformatic associations alone.

Overall, I do not think the manuscript is ready for acceptance in its present form. The biological theme is relevant and the cross-dataset effort is substantial, but the work currently reads as an extensive compendium of correlated analyses built around a stromal signature rather than a rigorously validated discovery of conserved regulators. A major revision would be necessary, with particular emphasis on external validation, clarification of the TCGA/GTEx integration strategy, stronger control for confounding in survival and diagnostic modeling, more disciplined interpretation of the single-cell data, and substantial moderation of the translational claims.

 

Author Response

Thank you for your careful review and insightful comments on our manuscript. Your observations are highly pertinent and directly address the core limitations of this study, including its overly descriptive nature, insufficient causal inference, and the lack of rigorous validation in certain analyses. We fully accept your concerns and will systematically address the issues you have raised in the revised manuscript. Our goal is to reposition the study from a broad correlation-based analysis toward a more cautious approach focused on descriptive findings and preliminary validation. Below are our point-by-point responses.
The revised portions of the manuscript have been highlighted in red.

Comments 1: The manuscript addresses an important and potentially interesting question, namely whether a conserved tumor-microenvironment program can be identified across multiple digestive cancers. The attempt to integrate bulk transcriptomics, WGCNA, scRNA-seq, mutation, methylation, splicing, immune correlation, drug sensitivity, and diagnostic modeling is ambitious, and the identification of a stromal/myeloid-centered signature is not in itself implausible. The main signal the study recovers, especially around ECM remodeling, fibroblast biology, and TREM2-associated myeloid biology, is biologically coherent. However, in its current form the work is considerably more descriptive than mechanistic, and several core analytical choices are not sufficiently rigorous to support the strength of the claims being made. In particular, the manuscript repeatedly moves from correlation to causation, and from pan-cancer association to translational promise, without the level of validation that would be needed for such conclusions.
Response 1: Thank you very much for your incisive summary. We fully agree that the original manuscript was overly assertive in its causal interpretations and translational claims, exceeding what can be supported by the current data.
To address this issue, we have systematically revised the entire manuscript by replacing strong causal statements such as “play important roles” and “key regulators” with more cautious and descriptive wording, such as “identified as candidate markers” and “may be associated with.”
In the Discussion section, we have also revised statements such as “provides valuable clues for personalized therapy” to “may offer preliminary associations that could be explored in future studies regarding personalized therapy.” Furthermore, we have reframed the positioning of our study to emphasize that it aims to “identify a conserved gene signature” and “provide a candidate gene set for future exploration,” rather than claiming direct clinical applicability.

Comments 2: My main concern is that the study design is heavily predisposed to rediscover a broad stromal/mesenchymal signal rather than a truly conserved regulatory program specific to digestive cancers. The authors begin by intersecting differential expression results across seven tumor types and then apply WGCNA to the shared 540 protein-coding genes, ultimately focusing on a 32-gene module enriched for ECM-related functions and strongly linked to stromal indices. Given that the input genes are already restricted to those consistently dysregulated across very different tissues, and given that tumor-versus-normal comparisons were built from TCGA plus GTEx data, it is not surprising that the dominant output is a fibroblast/ECM signature. In other words, the pipeline seems optimized to capture common stromal admixture rather than tumor-intrinsic conserved biology. This is especially important because the paper later interprets DCN, COL10A1, CTHRC1, and TREM2 as “key regulators,” whereas the data presented mainly show that these genes mark matrix CAF or myeloid abundance and correlate with stromal programs. The evidence provided does not establish regulatory hierarchy, only repeated association with known microenvironmental states.
Response 2: Thank you for identifying this key issue. We acknowledge that the analytical workflow in the original manuscript tends to capture stromal/microenvironment-associated signals. In response, we have made the following revisions:
We have redefined the four genes from “hub genes” and “key regulators” to “candidate markers” and “a conserved four-gene signature.” In Section 2.1 of the Results, we retain an objective description of the WGCNA analysis while avoiding overinterpretation of the identified module as a “regulatory program.” Additionally, statements such as “these genes play important roles in cancer” have been revised to more cautious descriptions, such as “the expression of these genes is associated with patient prognosis and they are localized to specific cell types at the single-cell level.”

Comments 3: A second major issue is the insufficient handling of confounding and model inflation in the clinical and diagnostic sections. The prognostic screening combines univariate Cox, multivariate Cox, LASSO, and random forest, and then takes the intersection to define four hub genes. That sounds rigorous on paper, but the manuscript does not clearly describe how covariates were handled across cancers, whether proportional hazards assumptions were checked, whether multicollinearity among ECM genes was assessed, or whether the multivariable model included standard clinicopathologic factors beyond survival endpoints and stage correlations. The same problem becomes even more serious in the diagnostic section. The logistic model is built and tested by random 70/30 splitting of the same TCGA+GTEx-derived matrix, and the manuscript highlights AUC values above 0.98 with sensitivity and specificity above 0.95. Without an external validation cohort, this is not convincing evidence of clinical utility; it is much more likely to reflect dataset-specific separation, tissue composition differences, and TCGA-versus-GTEx batch structure. The fact that the authors use TCGA and GTEx together for tumor-normal discrimination, yet do not present a strategy for harmonization beyond using Xena TPM values, is a serious weakness. A model trained under those conditions can easily learn platform and tissue-source differences rather than disease biology.
Response 3: Thank you for pointing out these methodological issues. We did not include cancer type as a covariate in the analysis because our objective was to investigate shared key genes and molecular mechanisms across digestive cancers. Therefore, we treated all digestive cancers as a single cohort to avoid artificially introducing categorical labels, considering that prognostic differences among cancers are largely influenced by gene-level factors. However, under this analytical framework, the selected genes should not be strictly referred to as independent prognostic genes, and we have revised the relevant descriptions in Section 2.3 accordingly.
In addition, we generated KM survival curves for these four genes across all digestive cancers and performed permutation tests; the results are presented in Supplementary Figure S2. Furthermore, in the logistic regression model construction, we conducted variance inflation factor (VIF) analysis, and all four genes showed VIF values below 5, indicating no significant multicollinearity (see Figure S11E).
We have also thoroughly revised the model construction section. Specifically, we used the TCGA dataset for model development and the GEO dataset for external validation, with batch effects corrected between the TCGA and GEO datasets. Given the imbalance between tumor and normal samples in the TCGA dataset, we applied both undersampling and oversampling to balance the training set. However, the validation set still contains a limited number of normal samples, which remains a limitation and has been acknowledged in the Discussion. The corresponding revisions can be found in Sections 2.7 and 4.11, as well as in Figure 11.

Comments 4: Related to this, the manuscript’s own supplementary data undermine some of the confidence of the translational claims. The text states that CTHRC1 alone shows AUC > 0.9 across all digestive cancers, but the supplementary ROC plots for the other genes show that performance is quite variable depending on the gene and cancer type, with clearly weak performance in some cohorts, for example COL10A1 in LIHC and STAD and combined analyses that are far less impressive than the main model narrative suggests. Likewise, the manuscript presents the four-gene model as broadly robust, but robustness is not the same thing as an internal split of one pooled dataset. The same caution applies to the drug-sensitivity section, where correlations with CTRP and GDSC IC50 values are presented as therapeutically suggestive. These are only expression–drug correlations from cell-line based resources accessed through GSCA, not functional validation, not tumor-context testing, and certainly not evidence for drug repurposing or patient stratification. Those claims should be toned down substantially.
Response 4: Thank you for pointing out these instances of overinterpretation. We have revised the manuscript to tone down the claims regarding the diagnostic model. Specifically, we no longer emphasize statements such as “CTHRC1 alone achieves an AUC > 0.9” or that the four-gene model is broadly robust. Instead, we objectively present the ROC curves for each gene (Figures 11H–K) and describe only the observed results in the Results section without extrapolating beyond the data.
In terms of drug sensitivity analysis, we have also softened the related claims. The original statements have been revised to: “the correlation between the expression of these genes and the IC50 values of various drugs may offer preliminary associations that could be explored in future studies regarding personalized therapy.”

Comments 5: The single-cell part is probably the strongest section conceptually, but it still needs tighter analysis and more careful language. The authors assembled six GEO scRNA-seq datasets covering six digestive cancers and conclude that DCN, COL10A1, and CTHRC1 are enriched in mCAFs while TREM2 is enriched in myeloid cells and at lower levels in apCAFs. That general pattern is believable and consistent with current biology. Still, the manuscript overstates what the presented analyses can support. The statement that consistent cell composition across samples indicates the phenomenon is “not due to batch effects” is not justified; similar composition does not exclude residual technical or dataset-driven bias. More importantly, the cell annotation framework is not described with enough depth to evaluate whether mCAF and apCAF assignments are robust across all six datasets, especially because these datasets differ in platform, disease context, sample quality, and depth. The use of Harmony, DoubletFinder, and canonical markers is fine as a starting point, but it is not a substitute for showing integrated quality metrics, batch mixing diagnostics, cluster stability, or dataset-wise reproducibility of the key expression patterns. In addition, the manuscript jumps from cell-type localization to functional claims about EMT, antigen presentation, and immune modulation without direct cell-cell communication, trajectory, regulon, or perturbation analyses. As written, the scRNA-seq results support cell-of-origin mapping of the signature, but not the stronger mechanistic model the discussion advances.
Response 5: Thank you for your detailed suggestions regarding the single-cell analysis. We have added cell–cell communication analysis as an important new component in the revised manuscript. Specifically, in Section 2.6, we present a comprehensive cell–cell communication analysis that systematically highlights the ECM–CD44 signaling axis between fibroblasts and myeloid cells. This provides evidence at the intercellular interaction level to support our functional inferences and helps propose a potential mechanistic model. In addition, the cellular composition across different samples is shown in Supplementary Figure S3.
Given the limited number of fibroblasts in each cancer type, we combined fibroblasts from all digestive cancer samples for joint analysis and re-performed normalization and related preprocessing steps. This strategy allows for better identification of distinct subpopulations and helps prevent small cell populations from being obscured or misclassified due to low cell numbers.

Comments 6: The multi-omics sections also need to be interpreted more cautiously. The SNV, CNV, methylation, alternative splicing, pathway-correlation, and immune-correlation analyses are presented one after another, but most remain associative overlays on the same four genes. For example, SNVs are reported to have little survival impact except in esophageal carcinoma, CNVs are said to influence survival, CTHRC1 methylation is negatively correlated with expression, and DCN splicing has opposite prognostic implications across tumor types. Rather than reinforcing a unified model, these results often point to context dependence and heterogeneity. Yet the discussion smooths over that heterogeneity and presents the four genes as conserved regulators with strong diagnostic, prognostic, and therapeutic potential. That conclusion is stronger than the data justify. A more accurate interpretation would be that the study identifies a recurrent stromal/myeloid-associated signature across digestive tumors, composed of genes with known relevance to ECM and immune biology, and that these genes deserve follow-up validation. That would still be useful, but it is a narrower and more defensible claim than the current framing.
Response 6: Thank you for raising this important point. We have softened the strength of our conclusions and revised the final paragraph of the Discussion accordingly. However, we would like to retain the term “Conserved” in the title. In the field of pan-cancer analysis, the term “conserved” is commonly used to describe molecular features that are consistently observed across multiple cancer types, rather than implying evolutionary conservation across species. Our use of “conserved” is consistent with this convention.
This usage is supported by multiple lines of evidence in our study: (1) the four-gene signature is consistently dysregulated across all seven digestive cancers; (2) single-cell RNA-seq analysis reveals stable cell-type localization patterns (DCN, COL10A1, and CTHRC1 in mCAFs, and TREM2 predominantly in myeloid cells) across different cancer types; (3) CellChat analysis identifies a conserved ECM–CD44 signaling axis present in each cancer type examined. Collectively, these findings suggest that the identified signature is not merely a technical artifact, but rather a reproducible biological feature shared across digestive cancers.

Comments 7: There are also multiple presentation and writing issues that need attention before publication. The manuscript contains a number of grammatical problems and overstatements, and some terminology is imprecise. For example, the methods section states that the “soft-power threshold was set to 0.9,” while the results and figure legend refer to a soft-thresholding power of 12, which is contradictory and needs correction. Figure labeling is occasionally awkward, and the writing repeatedly uses causal phrases such as “orchestrate tumor progression” or “key regulators” when only correlative evidence is shown. The abbreviation section and data availability statement are helpful, but the reproducibility standard is still not sufficient because the paper does not provide code, parameter settings in enough detail, or a transparent external validation workflow. If this manuscript is to be considered further, the authors should at minimum reframe the study more conservatively, correct methodological inconsistencies, provide stronger details for preprocessing and modeling, perform validation in truly independent cohorts, and avoid claiming diagnostic or therapeutic readiness from internal bioinformatic associations alone.
Response 7: Thank you for pointing out these specific issues. We have corrected the description of the WGCNA parameters: the soft-thresholding power was set to 12, which was selected based on achieving a scale-free topology fit index (R² = 0.9). The corresponding revisions are reflected in Section 4.2.
In addition, we have replaced overly strong expressions such as “orchestrate tumor progression” and “key regulators” with more cautious and appropriate wording.
Regarding the model construction section, as mentioned above, we have performed a comprehensive revision and added all necessary methodological details.

Comments 8: Overall, I do not think the manuscript is ready for acceptance in its present form. The biological theme is relevant and the cross-dataset effort is substantial, but the work currently reads as an extensive compendium of correlated analyses built around a stromal signature rather than a rigorously validated discovery of conserved regulators. A major revision would be necessary, with particular emphasis on external validation, clarification of the TCGA/GTEx integration strategy, stronger control for confounding in survival and diagnostic modeling, more disciplined interpretation of the single-cell data, and substantial moderation of the translational claims.
Response 8: Thank you again for your comprehensive and insightful review. In response to your suggestions, we have made the following revisions:
First, as described in “Response 3,” the model construction section has been fundamentally revised, including improvements in data processing and the addition of external validation.
Second, we have substantially toned down the conclusions of the study by replacing causal and exaggerated statements with more cautious and appropriate language.
Third, we have added cell–cell communication analysis to better support and strengthen the overall findings.
Finally, we have supplemented previously missing information such as AUC confidence intervals and corrected inconsistencies throughout the manuscript.

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

No additional comments

Reviewer 3 Report

Comments and Suggestions for Authors

The manuscript is ready for publication.