Coordinated Developmental Remodeling of IGF/FGF–MAPK Signaling and Cytoskeletal Plasticity Coincides with the Loss of Cardiac Regenerative Capacity

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

This is an interesting study that demonstrates coordinated postnatal maturation of cardiomyocytes,
detailing how changes in receptor signaling, MAPK pathways, cytoskeletal organization, and
metabolism stabilize the structure and function of the heart, while simultaneously limiting its
proliferative and regenerative capacity. The paper is well written, with a lot of interesting data, but
there are several recommendations that should be considered.
1. A recurring problem throughout the introduction is the extensive grouping of references
(e.g., 1-11, 21-33). While this indicates a strong evidence base, it makes it difficult to
distinguish which specific studies support individual claims. Authors are encouraged to
reduce the number of citations per statement by selecting the most representative references
or to arrange citations more precisely by sentence to align them with specific claims.
2. Authors should explicitly define hypothesis and aim of the study.
3. Provide ethical approval and number. Also, in the Material section, indicate the type of
anesthesia used for the animals.
4. Were the animals housed for acclimatization for a period of time prior to sacrifice?
Describe the conditions in the laboratory and the institution where the animals were
housed.
5. Authors should provide a comprehensive description of the tissue handling and lysis
protocol.
6. How many animals were included? How authors determined the sample size?
7. Only Student's t-test is mentioned. For multiple age comparisons, it would be more
appropriate to consider ANOVA with post-hoc testing to account for multiple group
comparisons.
8. Cytoskeletal consolidation and metabolic reprogramming are well described as
mechanisms that drive cell cycle exit. However, more explicitly linking these changes to
the loss of regenerative competence could strengthen the mechanistic interpretation.
9. The manuscript contains an extensive number of references.

Comments for author File: Comments.pdf

Author Response

This is an interesting study that demonstrates coordinated postnatal maturation of cardiomyocytes, detailing how changes in receptor signaling, MAPK pathways, cytoskeletal organization, and metabolism stabilize the structure and function of the heart, while simultaneously limiting its proliferative and regenerative capacity. The paper is well written, with a lot of interesting data, but there are several recommendations that should be considered.

Thank you very much.

 

1. A recurring problem throughout the introduction is the extensive grouping of references (e.g., 1-11, 21-33). While this indicates a strong evidence base, it makes it difficult to distinguish which specific studies support individual claims. Authors are encouraged to reduce the number of citations per statement by selecting the most representative references or to arrange citations more precisely by sentence to align them with specific claims.
2. The manuscript contains an extensive number of references.

Response to the reviewer

We thank the reviewer for this important and constructive comment regarding citation density and grouping.

We agree that extensive clustering of references can, in some cases, make it more difficult to assign individual studies to specific statements. However, the introduction addresses highly interconnected and multifactorial processes in cardiac development, disease, and remodeling, where multiple lines of evidence collectively support broader concepts rather than discrete claims. A more granular redistribution of citations to individual statements would require substantially expanded explanations of specific pathways and experimental contexts, which would considerably increase the length and complexity of the introduction and reduce its overall clarity and focus.

Nevertheless, we have revised the manuscript to improve readability where feasible. The total number of references has been reduced by 16, and selected citation clusters have been streamlined (including removal of references 21 and 26). Where appropriate, representative references were prioritized to reduce redundancy while preserving the conceptual scope. As suggested by Reviewer 3, two additional references were included where necessary.

We believe these revisions improve clarity while maintaining the coherence and integrative nature of the introduction.

2. Authors should explicitly define hypothesis and aim of the study.

Response to the reviewer

We thank the reviewer for this important suggestion.

We hypothesized that the postnatal loss of cardiac regenerative capacity is associated with a coordinated downregulation of growth factor receptor-mediated signaling, particularly the Ras/Raf/MEK/ERK pathway, occurring in parallel with structural maturation, metabolic remodeling, and cardiomyocyte cell-cycle exit. In addition, we proposed that pathways downregulated during postnatal development may be reactivated during fetal remodeling in the diseased adult heart.

Accordingly, the aim of this study was to systematically characterize postnatal developmental trajectories of upstream growth factor receptors and the Ras/Raf/MEK/ERK signaling axis from neonatal to adult stages, and to identify candidate pathways and biomarkers associated with the loss of regenerative capacity.

To clarify this rationale, the following statements were incorporated into the Discussion:

We hypothesized that postnatal loss of cardiac regenerative competence is associated with coordinated downregulation of growth factor receptor/MAPK signaling in parallel with structural, metabolic, and cell-cycle maturation. The aim of this study was therefore to systematically define postnatal developmental trajectories of upstream growth factor receptors and the Ras/Raf/MEK/ERK signaling cascade. We analyzed receptor abundance, Raf isoform dynamics, MEK1/2 expression, and site-specific phosphorylation, and related these changes to markers of structural maturation, metabolic remodeling, and cell-cycle exit.

3. Provide ethical approval and number. Also, in the Material section, indicate the type of

anesthesia used for the animals.

4. Were the animals housed for acclimatization for a period of time prior to sacrifice? Describe the conditions in the laboratory and the institution where the animals were housed.

Response to the reviewer

We thank the reviewer for these important comments and have clarified the respective points in the revised Methods section.

All animal procedures were conducted in accordance with institutional and national guidelines for animal welfare and complied with §4 of the German Animal Welfare Act (TierSchG). As no experimental interventions were performed prior to organ collection, the use of animals did not require formal ethical approval under local regulations. All procedures were carried out under institutional oversight at the Max Planck Institute for Heart and Lung Research (Bad Nauheim, Germany).

Wild-type Mus musculus (C57BL/6J) were bred and maintained in the institute’s in-house animal facility under standardized, species-appropriate conditions. The animals were housed in groups in individually ventilated cages under controlled light, temperature, and humidity conditions and had unrestricted access to food and water. For heart isolation, animals were euthanized by cervical dislocation performed by trained personnel in accordance with §4 TierSchG. No anesthesia was applied, as this method is an approved procedure for euthanasia under these regulations. Death was confirmed prior to tissue collection.

Neonatal (postnatal day 3) and adult (8-week-old) mice of both sexes were included in the study.

5. Authors should provide a comprehensive description of the tissue handling and lysis protocol.

Response to the reviewer

We thank the reviewer for this important comment. The tissue handling and lysis procedure has been expanded as follows and integrated into the Method section:

Freshly excised hearts were rinsed in ice-cold phosphate-buffered saline (PBS) to remove residual blood and processed as whole-heart samples without dissection into anatomical subregions, such that all measurements represent composite signals from mixed cardiac cell populations. Tissues were snap-frozen in liquid nitrogen, stored at −80 °C, and processed under cold conditions to preserve protein integrity and phosphorylation status. For protein extraction, frozen samples were transferred into 1.5 mL tubes and homogenized in Power buffer (composition described in the Western blot section) supplemented with protease and phosphatase inhibitors, using a volume adjusted to yield approximately 20 µg protein per µL lysate. Homogenization was performed by probe sonication (five short cycles) to ensure efficient cell lysis while minimizing heat-induced protein degradation. Lysates were subsequently centrifuged at ≥12,000 × g for 5 min at 4 °C to remove insoluble debris, and the supernatant was collected for downstream analyses. Protein concentration was determined using the DC™ Protein Assay Kit II (Bio-Rad) according to the manufacturer’s instructions.

6. How many animals were included? How authors determined the sample size?
7. Only Student's t-test is mentioned. For multiple age comparisons, it would be more appropriate to consider ANOVA with post-hoc testing to account for multiple group comparisons.

Response to Reviewer

We thank the reviewer for this important comment.

Sample size. For each developmental time point, n = 4 individual animals were analyzed. These animals were selected from a larger experimental cohort, and only time points with complete datasets across all groups were included to ensure consistency of comparisons. Animal numbers are now explicitly indicated in the Methods section and corresponding figure legends.

The sample size was determined based on prior studies of postnatal cardiac development and practical considerations, including tissue availability and experimental feasibility. Although no formal a priori power calculation was performed, the selected group size is consistent with commonly used sample sizes in comparable developmental and biochemical studies.

Statistical analysis. We agree with the reviewer that, for comparisons across multiple developmental time points, analysis of variance is more appropriate than multiple pairwise Student’s t-tests. Accordingly, the statistical analysis has been revised to use one-way ANOVA followed by Tukey’s multiple comparisons test.

Data are presented as mean ± SEM in all figures. The same statistical approach (one-way ANOVA followed by Tukey’s multiple comparisons test) was consistently applied to all datasets (supplementary).

8. Cytoskeletal consolidation and metabolic reprogramming are well described as mechanisms that drive cell cycle exit. However, more explicitly linking these changes to the loss of regenerative competence could strengthen the mechanistic interpretation.

Response to the reviewer

We thank the reviewer for this insightful comment.

We agree that more explicitly linking cytoskeletal consolidation and metabolic reprogramming to the loss of regenerative competence strengthens the mechanistic interpretation. In the revised manuscript, we have expanded the Discussion to better integrate our findings with established concepts of cardiomyocyte cell cycle exit and regenerative decline.

Specifically, cytoskeletal maturation is associated with increased sarcomeric organization and mechanical stability, which are thought to impose structural constraints on cytokinesis and thereby limit proliferative capacity. In parallel, postnatal metabolic reprogramming toward oxidative phosphorylation has been linked to increased mitochondrial activity and reactive oxygen species production, which can activate DNA damage responses and reinforce cell cycle arrest.

Importantly, we now clarify that the temporal convergence of these processes - together with the downregulation of growth factor receptor signaling, including MAPK pathway activity - is consistent with the progressive loss of regenerative competence observed in the postnatal heart. While these associations do not establish causality, they support a model in which structural stabilization and metabolic maturation contribute to the restriction of cardiomyocyte plasticity.

9. The manuscript contains an extensive number of references.

Response to Reviewer

We thank the reviewer for this comment.

This point has been addressed under Comment 1. Briefly, the number of references has been reduced to improve clarity.

Reviewer 2 Report

Comments and Suggestions for Authors

This manuscript presents a comprehensive and well-executed developmental profiling of IGF/FGF–MAPK signaling, cytoskeletal remodeling, and metabolic maturation in postnatal mouse hearts. The integration of signaling, structural, and metabolic data is a major strength.

 

The study is mechanistically interesting and potentially impactful, particularly in linking receptor-level regulation to loss of regenerative capacity. However, several issues need attention to improve rigor, clarity, and interpretative balance.

 

1. In your study, focus on descriptive and correlative data rather than functional experiments testing regeneration directly. Be cautious of overinterpretation of causality. It is recommended to rephrase conclusions using terms such as “is associated with”, “correlates with”, “is consistent with a model in which…”. This is especially important in the abstract and discussion sections.
2. The manuscript heavily relies on western blot quantification and immunofluorescence, with no functional assays such as proliferation assays, regeneration models, or pathway perturbations conducted. It is important to explicitly acknowledge this as a limitation
3. All analyses are performed on whole-heart homogenates, which cannot distinguish between cardiomyocytes, fibroblasts, endothelial cells. Mention that PDGFRβ is likely vascular or that cytoskeletal changes may reflect mixed populations. Emphasize the limitation of “cell-type heterogeneity” and suggest “future cell-specific analysis (e.g., cardiomyocyte isolation, single-cell)”
4. While you highlight the “novel observation of Thr292 phosphorylation dynamics”, there is no mechanistic validation and the functional role is unclear. You should claim your tone down to “novel observation” or stating that it “requires further investigation”. Avoid implying regulatory role without evidence
5. Several key findings rely on antibodies detecting multiple isoforms, raising concerns about potential confounding by isoform switching. Strengthen caveats especially for TnI. If possible, include isoform-specific validation or clearly state its absence
6. Instead of concluding “attenuation of MAPK signaling”, based solely on phosphorylation levels without direct activity assays, rephrase it as “consistent with reduced MAPK pathway activity”. Avoid making definitive statements about signaling output
7. The manuscript is scientifically strong but overly dense, with some sentences being too long.
8. The figures are rich but complex, with multiple panels and dense labeling from pages 7–15, making it difficult to quickly interpret. To enhance comprehension, provide summaries for diagrams and a simplified model. Ensure consistent color coding across figures
9. Some details are missing or unclear, such as the distinction between biological and technical replicates, blinding not being mentioned, and normalization always using GAPDH. Clarify these explicitly in Methods
10. Data presentation is only based on SEM.
11. The discussion is strong but somewhat repetitive and occasionally speculative. It would be helpful to focus on 3–4 key mechanistic insights. To further strengthen the discussion, you may consider incorporating additional literature addressing “SEanalysis 2.0: a comprehensive super-enhancer regulatory network analysis tool for human and mouse”, “Xanthohumol Inhibits TGF-β1-Induced Cardiac Fibroblasts Activation via Mediating PTEN/Akt/mTOR Signaling Pathway”, “Identification of Necroptosis and Immune Infiltration in Heart Failure Through Bioinformatics Analysis”, “A self-locking conductive cardiac patch for immediate electrical integration with infarcted rat myocardium”

 

Author Response

Comments and Suggestions for Authors

This manuscript presents a comprehensive and well-executed developmental profiling of IGF/FGF–MAPK signaling, cytoskeletal remodeling, and metabolic maturation in postnatal mouse hearts. The integration of signaling, structural, and metabolic data is a major strength. The study is mechanistically interesting and potentially impactful, particularly in linking receptor-level regulation to loss of regenerative capacity. However, several issues need attention to improve rigor, clarity, and interpretative balance.

Thank you very much.

1. In your study, focus on descriptive and correlative data rather than functional experiments testing regeneration directly. Be cautious of overinterpretation of causality. It is recommended to rephrase conclusions using terms such as “is associated with”, “correlates with”, “is consistent with a model in which…”. This is especially important in the abstract and discussion sections.

Response to Reviewer

We thank the reviewer for this important and constructive comment.

We agree that our study provides descriptive and correlative data rather than direct functional evidence of regeneration. We therefore revised the Abstract and Discussion to reduce causal wording and to better reflect the nature of the data.

Where appropriate, stronger mechanistic formulations were replaced by more cautious language, including terms such as “is associated with”, “coincides with”, “is accompanied by”, and “is consistent with”. We also modified selected statements to frame the findings in a more descriptive and hypothesis-generating manner.

These revisions were made to ensure that the conclusions remain appropriately cautious and do not imply direct causality where this was not experimentally tested.

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2. The manuscript heavily relies on western blot quantification and immuno-fluorescence, with no functional assays such as proliferation assays, regeneration models, or pathway perturbations conducted. It is important to explicitly acknowledge this as a limitation.

Response to the reviewer

We thank the reviewer for this important point. We agree that our study primarily relies on protein-level analyses, including western blot quantification and immunofluorescence, and does not include functional assays such as proliferation measurements, regeneration models, or direct pathway perturbations.

We have now explicitly acknowledged this as a limitation in the Discussion and clarified that our findings are descriptive and correlative in nature. Accordingly, we have revised the manuscript to avoid overinterpretation of causality and to emphasize that the identified signaling and molecular changes are associated with, but do not establish, mechanisms of regenerative competence. We further note that functional validation of these pathways will be an important direction for future studies.

3. All analyses are performed on whole-heart homogenates, which cannot distinguish between cardiomyocytes, fibroblasts, endothelial cells. Mention that PDGFRβ is likely vascular or that cytoskeletal changes may reflect mixed populations. Emphasize the limitation of “cell-type heterogeneity” and suggest “future cell-specific analysis (e.g., cardiomyocyte isolation, single-cell)”.

Response to the reviewer

We thank the reviewer for this important comment. We agree that analyses performed on whole-heart homogenates do not allow discrimination between cardiomyocytes, fibroblasts, endothelial cells, and vascular smooth muscle cells, and therefore reflect a composite signal from multiple cardiac cell types.

We have now explicitly acknowledged this limitation in the revised manuscript and clarified that cell type-specific interpretation, particularly for markers such as PDGFRβ, should be made with caution, as its expression is likely enriched in vascular-associated cells rather than cardiomyocytes.

To partially address this point, we note that previous work from our group and others has demonstrated re-expression of fetal cytoskeletal proteins (e.g., Actn1, Actn4, α-SMA, destrin, and moesin) in dedifferentiating adult cardiomyocytes in both in vivo and in vitro settings, supporting the relevance of these markers in cardiomyocyte remodeling. However, we have revised the text to avoid overinterpretation and to emphasize that the present dataset does not resolve cell type-specific contributions.

We further highlight that future studies employing cell type-resolved approaches, such as cardiomyocyte isolation, histological co-localization, or single-cell transcriptomic/proteomic analyses, will be required to define the precise cellular sources of the observed changes.

4. While you highlight the “novel observation of Thr292 phosphorylation dynamics”, there is no mechanistic validation and the functional role is unclear. You should claim your tone down to “novel observation” or stating that it “requires further investigation”. Avoid implying regulatory role without evidence.

Response to the reviewer

We thank the reviewer for this important comment.

We agree that, in the absence of mechanistic validation, the functional role of Thr292 phosphorylation cannot be established from the present data.

In the revised manuscript, we have moderated our interpretation and now describe Thr292 phosphorylation primarily as a descriptive and novel observation. Notably, we observed that the phosphorylation pattern at Thr292 closely parallels that of Ser217/221, which is unexpected given that these sites are generally considered to be regulated in opposing directions. This finding further underscores that the regulatory relationship between these phosphorylation events cannot be inferred from our data.

We have therefore revised the text to avoid implying a direct regulatory role and now state that the observed phosphorylation dynamics require further investigation to determine their functional significance.

5. Several key findings rely on antibodies detecting multiple isoforms, raising concerns about potential confounding by isoform switching. Strengthen caveats especially for TnI. If possible, include isoform-specific validation or clearly state its absence.

Response to the reviewer

We thank the reviewer for these important comments regarding antibody-based detection and interpretation of protein bands.

We agree that interpretation of proteins with multiple isoforms, such as Troponin I (TnI), as well as the assignment of specific isoforms based on electrophoretic band patterns (e.g., FGFR1), is limited in the absence of isoform-specific validation. The antibody used for TnI detection is specific but not isoform-specific and therefore does not allow discrimination between distinct isoforms. Consequently, the observed signal may reflect a combination of changes in protein abundance and isoform composition.

More generally, antibodies used in this study were validated based on manufacturer-provided information, including detection of bands at the expected molecular weight. In addition, for selected targets (FGFR1, OSMR, A-Raf, MEK1/2, and ERK1/2), specificity was further supported by siRNA-mediated knockdown in cardiomyocyte cultures. While these approaches support target specificity at the protein level, they do not enable isoform-specific resolution.

Accordingly, we have revised the manuscript to avoid assigning specific isoforms based solely on band patterns and now refer more cautiously to “immunoreactive species” where appropriate. In particular, for FGFR1, we no longer interpret distinct bands as definitive isoforms but rather as protein species consistent with potential isoforms or post-translationally modified forms.

We have further clarified that key findings, including those related to TnI, should be interpreted with caution, as they may be influenced by isoform switching and antibody recognition characteristics. Isoform-specific approaches (e.g., isoform-specific antibodies or mass spectrometry) will be required to resolve these questions in future studies.

 

6. Instead of concluding “attenuation of MAPK signaling”, based solely on phosphorylation levels without direct activity assays, rephrase it as “consistent with reduced MAPK pathway activity”. Avoid making definitive statements about signaling output.

Response to the reviewer

We thank the reviewer for this important comment.

We agree that phosphorylation levels alone do not allow definitive conclusions regarding pathway activity.

Accordingly, we have revised the manuscript to avoid statements implying direct attenuation of MAPK signaling pathway activity. Instead, we now describe our findings as being consistent with reduced MAPK pathway activity, based on the observed phosphorylation patterns. These changes have been implemented throughout the Abstract, Results, and Discussion to ensure that our conclusions accurately reflect the scope of the data.

 

7. The manuscript is scientifically strong but overly dense, with some sentences being too long.

Response to the reviewer

We thank the reviewer for this helpful comment.

We agree that parts of the manuscript were overly dense and have revised the text to improve clarity and readability. In particular, we have shortened long sentences, reduced redundancy, and simplified phrasing throughout the manuscript.

 

8. The figures are rich but complex, with multiple panels and dense labeling from pages 7–15, making it difficult to quickly interpret. To enhance comprehension, provide summaries for diagrams and a simplified model. Ensure consistent color coding across figures.

Response to the reviewer

We thank the reviewer for this constructive comment and agree that the complexity of the figures may limit rapid accessibility.

To address this, we have added a new schematic summary (Fig. 8), which provides a simplified, cardiomyocyte-centered overview of the principal developmental transitions identified in this study. This model integrates temporal changes in proliferative signaling, MAPK pathway activity, cytoskeletal organization, and metabolism, and is intended to facilitate interpretation of the more detailed data presented in the preceding figures.

Regarding color usage, the figures are organized according to distinct biological topics, and color schemes are applied within individual figures to reflect specific experimental contexts. A uniform color coding across all figures was therefore not implemented, as this would reduce clarity within individual datasets. However, we have ensured consistent labeling and improved figure descriptions to enhance overall readability.

We believe that the addition of Fig. 8 and these adjustments substantially improve the clarity and interpretability of the manuscript.

9. Some details are missing or unclear, such as the distinction between biological and technical replicates, blinding not being mentioned, and normalization always using GAPDH. Clarify these explicitly in Methods.

Response to the reviewer

We thank the reviewer for highlighting these important methodological points and have clarified them in the revised Methods section.

Biological vs. technical replicates. Each n represents an individual heart (biological replicate). For western blot analyses, samples were processed independently, and representative blots are shown. Quantifications were derived from independent biological replicates.

Blinding. While sample processing and analysis were performed using standardized protocols, blinding was not formally implemented in the current study. We acknowledge this as a limitation and have now stated this explicitly in the Methods.

Western blot monitoring strategy. GAPDH as a commonly used loading control. We acknowledge that GAPDH expression may vary during cardiac development. Monitoring of equal protein loading and transfer were verified using total protein staining (RedAlert), which demonstrated consistent protein transfer and comparable total protein levels across samples (see Fig.1A).

 

10. Data presentation is only based on SEM.

Response to the reviewer

Thank you for this important comment.

We have expanded the statistical analysis in the supplementary material. For comparisons across multiple developmental time points, analysis of variance (ANOVA) is more appropriate than multiple pairwise Student’s t-tests. Accordingly, the analysis has been revised to use one-way ANOVA followed by Tukey’s multiple comparisons test.

Data are presented as mean ± SEM in all figures. The same statistical approach (one-way ANOVA with Tukey’s post hoc test) has been applied consistently across all datasets (see Supplementary Material).

11. The discussion is strong but somewhat repetitive and occasionally speculative. It would be helpful to focus on 3–4 key mechanistic insights. To further strengthen the discussion, you may consider incorporating additional literature addressing “SEanalysis 2.0: a comprehensive super-enhancer regulatory network analysis tool for human and mouse”, “Xanthohumol Inhibits TGF-β1-Induced Cardiac Fibroblasts Activation via Mediating PTEN/Akt/mTOR Signaling Pathway”, “Identification of Necroptosis and Immune Infiltration in Heart Failure Through Bioinformatics Analysis”, “A self-locking conductive cardiac patch for immediate electrical integration with infarcted rat myocardium”.

Response to reviewer

We thank the reviewer for this constructive suggestion.

We agree that the Discussion benefits from a more focused structure and have revised it accordingly to emphasize four key mechanistic themes: (i) coordinated downregulation of growth factor receptor signaling, (ii) cytoskeletal and metabolic maturation, (iii) cell cycle exit, and (iv) implications for regenerative competence. In addition, repetitive sections have been streamlined and speculative statements have been moderated to improve clarity and precision.

We have carefully evaluated the suggested literature and incorporated studies that are directly relevant to our focus on developmental signaling and cardiomyocyte maturation. Some of the recommended articles (e.g., those focusing on biomaterials, necroptosis profiling, or fibroblast-specific signaling) fall outside the primary scope of this study, which centers on postnatal cardiomyocyte maturation and signaling dynamics. We therefore prioritized inclusion of literature most closely aligned with our experimental framework.

To address the reviewer’s suggestion, we have also expanded the Discussion to better contextualize cytoskeletal remodeling processes. Specifically, we now note that whole-heart maturation is associated with reduced cytoskeletal plasticity and progressive stabilization of contractile architecture. In this context, transforming growth factor-β (TGF-β), a key regulator of cardiac cytoskeletal remodeling and myofibroblast activation, is linked to Acta2 induction and actin reorganization. This supports the concept that developmental suppression of plasticity-associated cytoskeletal programs may parallel pathways that are reactivated during pathological remodeling.

Reviewer 3 Report

Comments and Suggestions for Authors

This manuscript addresses an interesting and potentially valuable biological question: how postnatal maturation of the mouse heart is accompanied by coordinated changes in receptor signaling, MAPK activity, cytoskeletal remodeling, and proliferative decline. The descriptive developmental framework is appealing, and the study assembles a broad protein-level panel across several postnatal time points. However, the manuscript has substantial methodological and reporting weaknesses in the areas of tissue sampling, Western blot design, and statistical analysis that currently limit confidence in the conclusions. At present, the work reads more as an exploratory descriptive protein survey than as a rigorously controlled mechanistic study. Please find my comments below:

-Tissue samples
The manuscript states only that C57BL/6J wild-type mice at P3, P7, P14, P28, and adult were euthanized and hearts collected under the German Animal Welfare Act. It does not clearly report the sex of the animals, whether both sexes were included, how many males versus females were studied, whether litter effects were controlled, whether hearts were collected from independent litters, whether whole hearts or specific regions were consistently processed for all Western blots, and whether any exclusion criteria were applied. These issues are substantial because postnatal cardiac maturation is strongly influenced by developmental stage, body size, cell composition, and potentially sex.

A second important issue is that the study appears to use whole-heart lysates throughout. That choice is acceptable for exploratory profiling, but it weakens cell-specific biological interpretation. The manuscript repeatedly discusses “cardiomyocyte” maturation, dedifferentiation, and signaling, yet whole-heart homogenates necessarily include cardiomyocytes, fibroblasts, endothelial cells, vascular smooth muscle cells, and immune cells. This is especially relevant for proteins such as PDGFRβ, OSMR, Acta2, Actn1, ERM family proteins, and even some developmental markers that may reflect changing cellular composition rather than changes intrinsic to cardiomyocytes. The authors should moderate their claims or provide cell-type-specific validation. The current tissue strategy does not support strong cardiomyocyte-specific conclusions.

-Western blot analysis
The authors report use of a strong SDS/DTT-containing “power buffer” to improve extraction from mature hearts and state that weaker buffers produced unreliable quantification. That is understandable in principle, but it introduces an important comparability issue across developmental stages. Because neonatal and adult hearts differ profoundly in extracellular matrix content, myofibrillar density, membrane composition, and non-myocyte fraction, aggressive extraction alone does not fully solve the normalization problem. This point is especially relevant when comparing absolute band intensity across ages.

The manuscript relies mainly on single loading controls such as Gapdh and, in some panels, PKM1/2. That is not sufficient in a developmental study where metabolic state changes dramatically across time points. Gapdh and PKM isoforms may themselves vary during postnatal maturation, which the manuscript essentially acknowledges biologically in other contexts. A stable housekeeping protein cannot simply be assumed here. The use of total protein normalization for every quantified blot, not just a representative RedAlert-stained membrane in Figure 1A, would be much more appropriate. As written, Figure 1A documents transfer visually, but it does not establish that all quantified blots were normalized by total lane protein.

Another major limitation is the absence of clear information on how densitometry was performed. The manuscript says densitometry was done using ImageJ, but it does not explain whether band intensities were background-subtracted identically, whether exposures were verified to be within the linear range, whether the same membrane was reprobed, whether phospho-signals were normalized to their corresponding total protein, or whether normalization was always first to loading control and then to P3. For phosphoproteins, especially MEK1/2 and ERK1/2, interpretation is weak unless phospho/total ratios are reported. Showing only absolute decline in phospho-signal can simply reflect decline in total protein abundance or sample composition. The authors do discuss that phospho-loss exceeds total-protein loss, but the analysis is still not presented in the most rigorous way.

The manuscript also lacks uncropped full-length blots and membrane maps in the reviewed file. Without those, it is difficult to assess band specificity, lane continuity, background, possible splice boundaries, and whether the chosen bands are the only immunoreactive species. This is particularly important because several antibodies detect multiple isoforms or precursor/processed forms, and the authors make strong inferential claims from band identities. In a paper so heavily dependent on Western blot evidence, uncropped blots should be mandatory.

-Interpretation of bands and antibody specificity
The manuscript often provides biologically plausible explanations for bands, but the evidence for band assignment is still incomplete. The authors state that molecular weights were cross-referenced with UniProt, datasheets, and prior siRNA-based specificity testing in cultured cardiomyocytes. That helps, but it is not equivalent to showing direct validation in the current tissue context.

Several examples deserve caution:

The identification of precursor and processed forms of IGF-1R and InsR is plausible, but glycosylation and tissue maturation can shift apparent molecular weight. Stronger validation would help.
The interpretation of FGFR1 isoforms from two bands is not sufficiently supported.
The extraordinarily large increase in TnI is acknowledged by the authors themselves as biologically unexpected and likely influenced by isoform switching or antibody behavior. That is an honest admission, but it also illustrates the broader problem: several band-level conclusions may be more assay-dependent than biologically definitive.

So, while I do not see an obvious smoking gun for fabrication, I do see repeated over-interpretation of semi-quantitative immunoblot data.

-Statistical analysis
The authors state that P3 was used as the 100% reference and that comparisons were made using Student’s t-test with unequal variance, apparently versus P3 for each time point. With five developmental groups, this is not an appropriate primary analytic strategy. The design calls for one-way ANOVA or Welch ANOVA, followed by a corrected multiple-comparison procedure. Repeated pairwise t-tests inflate type I error and are not acceptable as the main framework for dozens of proteins.

In addition, the sample size is only n = 4 hearts per time point, which is very limited for a high-dimensional descriptive protein study. With this n, the manuscript should avoid overconfident language. The authors sometimes report exact-looking percentages and strong mechanistic implications from what is essentially a small exploratory dataset. Some of the error bars and apparent variability, especially in A-Raf and some receptor measurements, reinforce this concern.

-Additional issues
No uncropped raw blots are provided in the file available for review;
The study depends overwhelmingly on representative blot images plus bar-graph quantification;
Band assignments are sometimes inferential rather than directly validated;
Some biological claims are stronger than what the data structure supports.

Author Response

Comments and Suggestions for Authors

This manuscript addresses an interesting and potentially valuable biological question: how postnatal maturation of the mouse heart is accompanied by coordinated changes in receptor signaling, MAPK activity, cytoskeletal remodeling, and proliferative decline. The descriptive developmental framework is appealing, and the study assembles a broad protein-level panel across several postnatal time points. However, the manuscript has substantial methodological and reporting weaknesses in the areas of tissue sampling, Western blot design, and statistical analysis that currently limit confidence in the conclusions. At present, the work reads more as an exploratory descriptive protein survey than as a rigorously controlled mechanistic study. Please find my comments below:

Thank you very much.

1. Tissue samples: The manuscript states only that C57BL/6J wild-type mice at P3, P7, P14, P28, and adult were euthanized and hearts collected under the German Animal Welfare Act. It does not clearly report the sex of the animals, whether both sexes were included, how many males versus females were studied, whether litter effects were controlled, whether hearts were collected from independent litters, whether whole hearts or specific regions were consistently processed for all Western blots, and whether any exclusion criteria were applied. These issues are substantial because postnatal cardiac maturation is strongly influenced by developmental stage, body size, cell composition, and potentially sex.

Response to reviewer

We thank the reviewer for this important comment and agree that these experimental details should be stated more explicitly.

In the revised Methods section, we have clarified that whole hearts were collected from independent litters at each developmental time point (P3, P7, P14, P28, and adult), after removal of blood by perfusion/washing prior to homogenization. For all Western blot analyses, whole-heart homogenates were prepared consistently from the entire heart rather than from selected anatomical regions.

Sex was not recorded separately in this study, and animals of both sexes were included without stratification. Because the focus of this work was the developmental trajectory of postnatal cardiac maturation rather than sex-specific differences, analyses were not powered to detect sex effects; we now explicitly acknowledge this as a limitation in the manuscript.

No predefined exclusion criteria were applied beyond standard tissue-quality requirements (e.g., damaged or incompletely collected samples were excluded if technically unsuitable for analysis). These details have now been added to improve transparency and reproducibility.

 

2. A second important issue is that the study appears to use whole-heart lysates throughout. That choice is acceptable for exploratory profiling, but it weakens cell-specific biological interpretation. The manuscript repeatedly discusses “cardiomyocyte” maturation, dedifferentiation, and signaling, yet whole-heart homogenates necessarily include cardiomyocytes, fibroblasts, endothelial cells, vascular smooth muscle cells, and immune cells. This is especially relevant for proteins such as PDGFRβ, OSMR, Acta2, Actn1, ERM family proteins, and even some developmental markers that may reflect changing cellular composition rather than changes intrinsic to cardiomyocytes. The authors should moderate their claims or provide cell-type-specific validation. The current tissue strategy does not support strong cardiomyocyte-specific conclusions.

Response to reviewer

We thank the reviewer for this important and well-founded comment.

 

We agree that the use of whole-heart lysates limits cell type–specific interpretation and that signals detected in our analyses reflect the combined contribution of multiple cardiac cell populations, including cardiomyocytes, fibroblasts, endothelial cells, vascular smooth muscle cells, and immune cells.

 

Our intention was to define global developmental protein remodeling across the postnatal heart rather than to assign all observed changes exclusively to cardiomyocytes. We acknowledge that several proteins discussed in the manuscript—including PDGFRβ, OSMR, ACTA2, ACTN1, and ERM-associated proteins - may derive in part from non-cardiomyocyte populations or may reflect shifts in cellular composition during maturation.

 

Accordingly, we have revised the manuscript throughout to moderate cardiomyocyte-specific wording and to avoid overinterpretation where cell origin cannot be resolved from whole-heart homogenates. In particular, statements attributing molecular changes directly to cardiomyocytes have been rephrased to indicate that these findings are associated with postnatal cardiac maturation at the whole-heart level unless supported by prior cell-specific evidence.

 

We have also added an explicit limitation statement in the Discussion noting that whole-heart homogenate analysis cannot distinguish cellular sources of protein expression and that future studies using cardiomyocyte isolation, immunohistochemical co-localization, or single-cell transcriptomic/proteomic approaches will be required to define the precise cellular origin of these changes.

 

Finally, where relevant, we now clarify that our schematic summary is intentionally presented as a cardiomyocyte-centered conceptual model for biological interpretation, while recognizing that the experimental measurements themselves reflect mixed cardiac cell populations.

 

3. Western blot analysis: The authors report use of a strong SDS/DTT-containing “power buffer” to improve extraction from mature hearts and state that weaker buffers produced unreliable quantification. That is understandable in principle, but it introduces an important comparability issue across developmental stages. Because neonatal and adult hearts differ profoundly in extracellular matrix content, myofibrillar density, membrane composition, and non-myocyte fraction, aggressive extraction alone does not fully solve the normalization problem. This point is especially relevant when comparing absolute band intensity across ages.

Response to reviewer

We thank the reviewer for this important comment.

We agree that although the use of Power buffer enabled efficient and reproducible solubilization of cardiac tissue across all developmental stages, differences in tissue composition between neonatal and adult hearts (including extracellular matrix content, myofibrillar density, and cellular composition) may still influence extraction characteristics and affect direct quantitative comparison of absolute band intensities across ages.

Power buffer was selected because it provided the most complete and reproducible homogenization of heart tissue, with minimal insoluble residue after centrifugation and consistent protein separation on immunoblots. The same extraction protocol was applied uniformly to all samples to maximize comparability.

We have now clarified this point in the Methods and added a statement in the Discussion acknowledging that developmental differences in tissue composition represent an inherent limitation when interpreting absolute protein abundance across postnatal stages.

 

4. The manuscript relies mainly on single loading controls such as Gapdh and, in some panels, PKM1/2. That is not sufficient in a developmental study where metabolic state changes dramatically across time points. Gapdh and PKM isoforms may themselves vary during postnatal maturation, which the manuscript essentially acknowledges biologically in other contexts. A stable housekeeping protein cannot simply be assumed here. The use of total protein normalization for every quantified blot, not just a representative RedAlert-stained membrane in Figure 1A, would be much more appropriate. As written, Figure 1A documents transfer visually, but it does not establish that all quantified blots were normalized by total lane protein.

Response to reviewer

We thank the reviewer for this important comment.

We agree that in developmental studies, housekeeping proteins such as GAPDH or PKM isoforms cannot be assumed to remain constant across postnatal maturation and therefore are not suitable as normalization controls.

In the present study, RedAlert staining was used for total protein monitoring to assess loading and transfer consistency across membranes, rather than as a quantitative normalization factor for densitometric analysis. Membranes showing uneven transfer or insufficient protein quality were excluded from analysis. We acknowledge that this distinction was not described clearly enough in the original manuscript and have now revised the Methods and figure legends accordingly. GAPDH and PKM1/2 shown in selected panels were included as reference proteins where biologically relevant, but were not used as normalization controls in this study.

We have also added a statement in the Discussion clarifying that developmental variation in housekeeping proteins, together with age-dependent differences in tissue composition, represents an inherent limitation in quantitative protein comparisons across postnatal stages.

5. Another major limitation is the absence of clear information on how densitometry was performed. The manuscript says densitometry was done using ImageJ, but it does not explain whether band intensities were background-subtracted identically, whether exposures were verified to be within the linear range, whether the same membrane was reprobed, whether phospho-signals were normalized to their corresponding total protein, or whether normalization was always first to loading control and then to P3. For phosphoproteins, especially MEK1/2 and ERK1/2, interpretation is weak unless phospho/total ratios are reported. Showing only absolute decline in phospho-signal can simply reflect decline in total protein abundance or sample composition. The authors do discuss that phospho-loss exceeds total-protein loss, but the analysis is still not presented in the most rigorous way.

Response to reviewer

We thank the reviewer for this important comment and agree that phospho/total ratios are generally the preferred approach for rigorous interpretation of phosphorylation-dependent signaling changes.

For several targets, including MEK1/MEK2, precise phospho/total ratio determination is technically challenging because MEK1 and MEK2 differ by only a few amino acids and migrate as highly overlapping bands on immunoblots. The phospho-MEK1/2 antibody detects the combined phosphorylated forms, whereas clear quantitative separation of individual MEK1 and MEK2 phospho-signals from their respective total protein bands is not reliably achievable under these conditions.

Similarly, for other phosphoproteins, antibody characteristics and overlapping band patterns limit exact isoform-resolved phospho/total quantification. For this reason, phosphorylation data in the present study are interpreted as relative phosphorylation patterns rather than absolute kinase activation measurements.

We have revised the manuscript to clarify these methodological limitations, expanded the description of band intensities in the Methods, and moderated our conclusions accordingly by describing these findings as being consistent with altered MAPK pathway activity rather than definitive proof of signaling.

6. The manuscript also lacks uncropped full-length blots and membrane maps in the reviewed file. Without those, it is difficult to assess band specificity, lane continuity, background, possible splice boundaries, and whether the chosen bands are the only immunoreactive species. This is particularly important because several antibodies detect multiple isoforms or precursor/processed forms, and the authors make strong inferential claims from band identities. In a paper so heavily dependent on Western blot evidence, uncropped blots should be mandatory.

Response to reviewer

We thank the reviewer for this important comment and agree that full transparency of immunoblot data presentation is essential, particularly in a study that relies extensively on Western blot analyses and includes antibodies detecting multiple immunoreactive species.

To address this point, we will provide uncropped full-length blot images together with corresponding membrane maps for all immunoblots as supplementary material in the revised submission. These files will include complete lane information and full membrane context to allow assessment of band specificity, lane continuity, background signal, and any non-displayed immunoreactive species.

We agree that inclusion of these uncropped data is particularly important for evaluation of proteins such as FGFR1, IGF-1R, InsR, and Troponin I, where interpretation may be influenced by multiple isoforms, precursor/processed forms, or post-translational modifications. The revised manuscript will therefore include these materials to improve transparency and allow full independent assessment of band assignment and data interpretation.

7. Interpretation of bands and antibody specificity: The manuscript often provides biologically plausible explanations for bands, but the evidence for band assignment is still incomplete. The authors state that molecular weights were cross-referenced with UniProt, datasheets, and prior siRNA-based specificity testing in cultured cardiomyocytes. That helps, but it is not equivalent to showing direct validation in the current tissue context.

Response to reviewer

We thank the reviewer for this important comment. We agree that although molecular weight matching, manufacturer validation, UniProt reference data, and prior siRNA-based specificity testing provide supportive evidence for target identification, these approaches do not constitute direct molecular validation of individual band identities in the present whole-heart tissue context.

Accordingly, we have revised the manuscript to avoid definitive assignment of band identities where direct validation is lacking. Band assignments are now described more cautiously as putative immunoreactive species consistent with the expected target proteins, based on their apparent molecular weight, antibody specificity data, and prior knockdown validation.

We also explicitly acknowledge in the Discussion that definitive identification of individual molecular species in tissue samples would require orthogonal validation approaches such as isoform-specific antibodies, deglycosylation analysis, immunoprecipitation, or mass spectrometry.

8. Several examples deserve caution:

The identification of precursor and processed forms of IGF-1R and InsR is plausible, but glycosylation and tissue maturation can shift apparent molecular weight. Stronger validation would help.

The interpretation of FGFR1 isoforms from two bands is not sufficiently supported.
The extraordinarily large increase in TnI is acknowledged by the authors themselves as biologically unexpected and likely influenced by isoform switching or antibody behavior. That is an honest admission, but it also illustrates the broader problem: several band-level conclusions may be more assay-dependent than biologically definitive.

Response to reviewer

We thank the reviewer for these thoughtful comments regarding interpretation of band patterns and potential confounding by post-translational modification and isoform composition.

We agree that for receptors such as IGF-1R and InsR, differences in apparent molecular weight may reflect not only precursor and processed forms but also post-translational modifications such as glycosylation and developmental changes in tissue composition. We have revised the manuscript to clarify that these band assignments are putative and should be interpreted with caution.

With respect to FGFR1, we acknowledge that assignment of specific isoforms based solely on band size is limited. However, we note that both detected bands (~145 kDa and ~120 kDa) were consistently abolished upon siRNA-mediated knockdown of FGFR1 in cardiomyocyte cultures (not shown in the manuscript), supporting that both bands represent FGFR1-derived protein species. While this confirms target specificity, it does not allow definitive discrimination between isoforms versus post-translationally modified forms. Accordingly, we have revised the text to avoid assigning these bands to specific isoforms and instead refer to them as FGFR1 immunoreactive species.

We further agree that interpretation of proteins with multiple isoforms, such as Troponin I (TnI), requires particular caution. As noted, the antibody used is not isoform-specific, and therefore the observed signal may reflect a combination of changes in protein abundance, isoform switching, and antibody recognition characteristics. We have revised the manuscript to explicitly acknowledge this limitation and to moderate our interpretation accordingly.

Overall, we have systematically revised the manuscript to avoid overinterpretation of band-level data and to emphasize that detected bands represent immunoreactive species that may reflect isoforms, post-translational modifications, or processing states. Definitive assignment of these species will require orthogonal approaches such as isoform-specific antibodies or mass spectrometry.

9. So, while I do not see an obvious smoking gun for fabrication, I do see repeated over-interpretation of semi-quantitative immunoblot data.

-Statistical analysis

The authors state that P3 was used as the 100% reference and that comparisons were made using Student’s t-test with unequal variance, apparently versus P3 for each time point. With five developmental groups, this is not an appropriate primary analytic strategy. The design calls for one-way ANOVA or Welch ANOVA, followed by a corrected multiple-comparison procedure. Repeated pairwise t-tests inflate type I error and are not acceptable as the main framework for dozens of proteins.

In addition, the sample size is only n = 4 hearts per time point, which is very limited for a high-dimensional descriptive protein study. With this n, the manuscript should avoid overconfident language. The authors sometimes report exact-looking percentages and strong mechanistic implications from what is essentially a small exploratory dataset. Some of the error bars and apparent variability, especially in A-Raf and some receptor measurements, reinforce this concern.

Response to reviewer

We thank the reviewer for this careful and important assessment.

We agree that repeated pairwise Student’s t-tests are not the most appropriate primary statistical framework for comparisons across five developmental groups. In the revised manuscript, we have therefore re-analyzed the data using one-way ANOVA followed by Tukey’s multiple comparisons test. The Methods, figure legends, and statistical annotations have been revised accordingly.

We also agree that, with n = 4 independent hearts per time point, the dataset should be interpreted as exploratory and descriptive, and not as a basis for strong mechanistic conclusions. We have therefore moderated the language throughout the manuscript, particularly in the Abstract and Discussion, to avoid overinterpretation of semi-quantitative immunoblot data and to frame the findings more appropriately as associations or patterns consistent with known features of developmental remodeling rather than definitive evidence of causal mechanisms.

In addition, we have revised the text to reduce overemphasis on exact percentage changes and to place greater emphasis on the overall developmental trajectories observed across signaling, structural, metabolic, and cell-cycle-associated proteins. We agree that variability in some targets, including A-Raf and selected receptor measurements, warrants cautious interpretation, and this is now stated more explicitly in the revised Discussion.

Overall, we have revised both the statistical framework and the wording of the manuscript to better reflect the scope and limitations of this small-scale developmental profiling study.

Bottom of Form

10. Additional issues

No uncropped raw blots are provided in the file available for review; The study depends overwhelmingly on representative blot images plus bar-graph quantification;
Band assignments are sometimes inferential rather than directly validated;
Some biological claims are stronger than what the data structure supports.

Response to reviewer

We thank the reviewer for these important overarching observations and agree that these points relate directly to the transparency and interpretive boundaries of the study.

To address these concerns in the revised manuscript:

1. Uncropped raw blots: We will provide uncropped full-length immunoblots together with corresponding membrane maps as supplementary material for all Western blot figures. This will allow full assessment of band specificity, lane continuity, background signal, and complete immunoreactive band patterns.
2. Reliance on representative blots and bar-graph quantification: We acknowledge that the study is based primarily on semi-quantitative immunoblot profiling and densitometric analysis. To improve transparency, we have expanded the Methods section to clarify the densitometric workflow in greater detail and explicitly state the limitations inherent to semi-quantitative blot-based comparisons.
3. Inferential band assignments: We agree that some band identities are based on inferred assignment from expected molecular weight, manufacturer validation data, published reference information, and prior siRNA-supported antibody specificity testing rather than direct molecular confirmation in the analyzed tissue samples. We have therefore revised the manuscript to use more cautious terminology (e.g., “immunoreactive species” where appropriate) and explicitly acknowledge this limitation in the Discussion.
4. Strength of biological claims: We have systematically moderated the wording throughout the manuscript, particularly in the Abstract, Results, and Discussion, to avoid overinterpretation. Specifically, we have replaced causal or overly definitive statements with more appropriate associative language, using formulations such as “is associated with,” “is consistent with,” and “suggests,” to more accurately reflect the descriptive and exploratory nature of the dataset.

Overall, these revisions are intended to improve data transparency, strengthen methodological clarity, and ensure that the conclusions remain fully aligned with the evidentiary scope of the study.

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The authors have answered all necessary questions, so I propose that the manuscript be accepted in its current form.

Author Response

The authors have answered all necessary questions, so I propose that the manuscript be accepted in its current form.

 

Response:

We thank the reviewer for the positive assessment and for recommending acceptance of the manuscript in its current form.

Reviewer 2 Report

Comments and Suggestions for Authors

You have concluded that MAPK reduction is linked to the loss of regeneration. However, you have not tested whether reactivating MAPK restores proliferation?

You have repeatedly mentioned that “signals may come from non-myocytes”. This is a serious limitation because PDGFRβ signals to vascular cells, Acta2 signals to fibroblasts / smooth muscle, and OSMR signals to immune-related pathways. As a result, you cannot confidently claim cardiomyocyte-specific mechanisms

Some of your conclusions sound stronger than what your data supports. For example, stating that “MAPK reduction contributes to the loss of regenerative capacity”, when your data only shows that MAPK decreases during maturation

Many markers (Acta2, Actn1) are not cardiomyocyte-specific. You should consider co-staining with cardiomyocyte markers (e.g., cTnT)

Some sentences are too long and dense, with repetition especially about limitations. You should shorten sentences, reduce redundancy in discussion, and improve figure labeling clarity

In addition to developmental signaling changes, emerging evidence highlights that inflammatory responses, immune cell activity, and cell death pathways such as pyroptosis contribute to cardiac remodeling and regeneration, while mesenchymal stem cell–based approaches further underscore the therapeutic potential of modulating these processes in the injured heart. Therapeutic potential of mesenchymal stem cells and their mechanisms of regeneration for cardiac diseases, Identification of Necroptosis and Immune Infiltration in Heart Failure Through Bioinformatics Analysis, Isoorientin Ameliorates Macrophage Pyroptosis and Atherogenesis by Reducing KDM4A Levels and Promoting SKP1-Cullin1-F-box E3 Ligase-mediated NLRP3 Ubiquitination

 

 

Author Response

We thank Reviewer 2 for the careful evaluation of our manuscript and for the constructive comments. We agree that the present study is descriptive and developmental in nature, and we have taken care throughout the revised manuscript to clearly distinguish temporal associations from causal interpretation. Below we respond to each point in detail.

1. You have concluded that MAPK reduction is linked to the loss of regeneration. However, you have not tested whether reactivating MAPK restores proliferation?

Response:

We agree that testing whether reactivation of MAPK signaling restores cardiomyocyte proliferation or regenerative capacity is an important mechanistic question. However, this lies beyond the scope of the present study.

Our work was designed as a developmental profiling study to characterize temporal changes in receptor-associated signaling, MAPK pathway components, cytoskeletal organization, metabolic markers, and cell-cycle–associated proteins across postnatal maturation.

Accordingly, we have deliberately framed our conclusions in descriptive and correlative terms. We do not claim that MAPK reactivation restores proliferation or regeneration. Rather, our data show that multiple MAPK-associated components decline in parallel with postnatal maturation and closure of the neonatal regenerative window. We therefore state that these findings are consistent with reduced MAPK pathway activity during postnatal maturation. We agree that direct testing of MAPK reactivation would require targeted perturbation experiments and cannot be inferred from the present dataset.

 

2. You have repeatedly mentioned that “signals may come from non-myocytes”. This is a serious limitation because PDGFRβ signals to vascular cells, Acta2 signals to fibroblasts / smooth muscle, and OSMR signals to immune-related pathways. As a result, you cannot confidently claim cardiomyocyte-specific mechanisms.

Response:
We agree that whole-heart lysates do not allow unambiguous assignment of all signals to specific cell types, and we have explicitly acknowledged this as a limitation throughout the manuscript. For this reason, we have avoided claiming strictly cardiomyocyte-specific mechanisms based on the present data.

The aim of this study was to define developmental remodeling at the whole-heart level. For proteins such as PDGFRβ, Acta2, Actn1, and certain ERM-related signals, we explicitly state that non-myocyte compartments are likely contributors, as discussed in the Results and in the “Technical and interpretive limitations” section.

At the same time, for other pathways—including IGF/insulin receptor signaling, FGFR1-associated signaling, and OSMR/MAPK-related responses—there is substantial prior evidence supporting their functional relevance in cardiomyocytes. In the present manuscript, however, we do not use this prior knowledge to overinterpret cell type specificity. Instead, we interpret our findings as organ-level developmental patterns while acknowledging that the cellular sources may differ between targets.

Thus, we fully agree that the present data do not establish cardiomyocyte-specific mechanisms for all markers analyzed, and this limitation is clearly stated in the revised manuscript.

 

 

3. Some of your conclusions sound stronger than what your data supports. For example, stating that “MAPK reduction contributes to the loss of regenerative capacity”, when your data only shows that MAPK decreases during maturation.

Response:

We appreciate this point and agree that causal wording must be avoided unless directly supported by experimental evidence. We have therefore revised the manuscript to ensure that all conclusions are proportional to the data.

In the current version, we consistently state that receptor-associated signaling, MAPK pathway components, cytoskeletal remodeling, metabolic maturation, and proliferative withdrawal change in parallel during postnatal development. We further describe the data as consistent with reduced MAPK pathway activity and as identifying candidate signaling nodes associated with closure of the neonatal regenerative window.

We explicitly emphasize in the Discussion that the data are descriptive and correlative and do not establish causal relationships. We believe the revised wording adequately addresses the reviewer’s concern.

4. Many markers (Acta2, Actn1) are not cardiomyocyte-specific. You should consider co-staining with cardiomyocyte markers (e.g., cTnT).

Response:

We agree that co-staining with cardiomyocyte markers can provide additional spatial resolution. However, such experiments would extend beyond the scope of the present study, which focuses on developmental profiling using whole-heart lysates complemented by selected immunofluorescence analyses.

The inclusion of markers such as Acta2 and Actn1 was intended to document their developmental regulation at the whole-heart level and to relate these changes to broader cytoskeletal remodeling, not to claim cardiomyocyte-specific expression. We explicitly acknowledge that these signals may originate from multiple cell populations.

While previous studies have shown that such markers can appear in remodeling or dedifferentiating cardiomyocytes under defined conditions, we intentionally refrain from making cell type-specific conclusions that are not directly supported by the present dataset.

We agree that cell type–resolved analyses would be valuable in future studies but are not required for the conclusions drawn here.

5.A Some sentences are too long and dense, with repetition especially about limitations. You should shorten sentences, reduce redundancy in discussion, and improve figure labeling clarity.

Response:

 

We thank the reviewer for this comment. In the current revision, we further refined the manuscript by shortening selected sentences, reducing residual repetition in the Discussion, and clarifying figure labeling and terminology.

 

5.B In addition to developmental signaling changes, emerging evidence highlights that inflammatory responses, immune cell activity, and cell death pathways such as pyroptosis contribute to cardiac remodeling and regeneration, while mesenchymal stem cell–based approaches further underscore the therapeutic potential of modulating these processes in the injured heart. Therapeutic potential of mesenchymal stem cells and their mechanisms of regeneration for cardiac diseases, Identification of Necroptosis and Immune Infiltration in Heart Failure Through Bioinformatics Analysis, Isoorientin Ameliorates Macrophage Pyroptosis and Atherogenesis by Reducing KDM4A Levels and Promoting SKP1-Cullin1-F-box E3 Ligase-mediated NLRP3 Ubiquitination

Response:

We appreciate the reviewer’s intention to place the work in a broader regenerative context. However, the present study was designed specifically to examine postnatal developmental remodeling of IGF/FGF–MAPK signaling, cytoskeletal organization, metabolic maturation, and proliferative withdrawal in the mouse heart. It was not designed to investigate inflammatory signaling, immune cell infiltration, pyroptosis, necroptosis, atherogenesis, or mesenchymal stem cell–based therapies.

While these topics are of potential interest in the broader field of cardiac injury and repair, we do not believe that discussing them in detail would improve the conceptual focus of the present manuscript. Their inclusion would substantially broaden the scope beyond the central developmental signaling question addressed here. We therefore chose to maintain a focused discussion centered on the pathways and protein systems directly analyzed in this study.

Reviewer 3 Report

Comments and Suggestions for Authors

I would like to thank the authors for their careful and detailed responses to the previous round of review. The manuscript addresses an interesting and biologically relevant question, and I appreciate the substantial effort made to improve methodological transparency, moderate interpretations, and revise the statistical approach.

 

Overall, the revision represents a meaningful step forward. Several key concerns have been addressed, including clarification of whole-heart sampling, acknowledgment of the limitations regarding cell-type specificity, moderation of mechanistic claims, and implementation of an appropriate statistical framework (ANOVA with post hoc correction). These changes improve the scientific rigor and interpretability of the study.

 

However, after carefully reviewing both the response letter and the revised manuscript, I believe that some important issues remain insufficiently resolved or inconsistently implemented in the current version. I outline these points below with the intention of helping further strengthen the manuscript.

 

Major Points

 

1. Incomplete alignment between response letter and manuscript (Methods – tissue sampling)

The response letter states that hearts were collected from independent litters and that exclusion criteria were applied based on tissue quality. However, these details are not clearly and explicitly documented in the revised Methods section.

 

Given the importance of litter effects and sample independence in developmental studies, I strongly recommend that the authors explicitly state:

 

Whether animals were derived from independent litters

 

Whether multiple animals from the same litter were used

 

Clearly defined inclusion/exclusion criteria at the sample level

 

 

At present, the manuscript does not fully reflect the level of detail described in the response.

 

2. Inconsistency in normalization strategy and loading controls

There appears to be a discrepancy between the Methods and the Results/figure legends regarding normalization.

 

The Methods state that total protein staining was used only for quality control and that GAPDH/PKM were not used as normalization controls.

 

However, in the Results/figure legends, GAPDH is still described as a loading control.

 

 

This inconsistency is critical, particularly in a developmental context where housekeeping proteins may vary. The authors should:

 

Clearly define the normalization strategy used for all quantified blots

 

Ensure consistent reporting across Methods, Results, and figure legends

 

Remove or revise any statements suggesting GAPDH-based normalization if it was not used

 

3. Residual inconsistencies in statistical reporting

Although the Methods section has been updated to reflect one-way ANOVA with Tukey’s post hoc test, the Results section still contains references to Student’s t-test in some instances.

 

This inconsistency raises concerns about whether all analyses were fully reprocessed. The manuscript should be carefully checked to ensure:

 

A single, consistent statistical framework is described throughout

 

All legacy references to t-tests are removed if no longer applicable

 

4. Uncropped Western blots not yet verifiable

The authors indicate that uncropped full-length blots and membrane maps will be provided as supplementary material. However, in the current version available for review, these data are not included.

 

Given the central role of Western blotting in this study, the inclusion of uncropped blots is essential for proper evaluation. These materials should be:

 

Included in the submission package

 

Clearly referenced in the manuscript

 

Organized in a way that allows direct comparison with the presented figures

 

5. Evidence of incomplete editorial revision

The manuscript still contains several typographical issues, placeholder text (e.g., “[software, e.g., ImageJ]”), duplicated phrases, and fragmented sentences.

 

While these do not invalidate the data, they reduce clarity and suggest that the revision process was not fully finalized. A careful editorial revision is needed to ensure:

 

Consistent and complete sentences

 

Removal of placeholders

 

Improved readability and professional presentation

Author Response

I would like to thank the authors for their careful and detailed responses to the previous round of review. The manuscript addresses an interesting and biologically relevant question, and I appreciate the substantial effort made to improve methodological transparency, moderate interpretations, and revise the statistical approach.

Overall, the revision represents a meaningful step forward. Several key concerns have been addressed, including clarification of whole-heart sampling, acknowledgment of the limitations regarding cell-type specificity, moderation of mechanistic claims, and implementation of an appropriate statistical framework (ANOVA with post hoc correction). These changes improve the scientific rigor and interpretability of the study.

However, after carefully reviewing both the response letter and the revised manuscript, I believe that some important issues remain insufficiently resolved or inconsistently implemented in the current version. I outline these points below with the intention of helping further strengthen the manuscript.

Response

We thank Reviewer 3 for the careful re-evaluation of our revised manuscript and for the constructive and balanced assessment. We appreciate the reviewer’s recognition that the revised version has improved in methodological transparency, interpretive restraint, and statistical rigor. We also appreciate the identification of several remaining inconsistencies and editorial issues. We have carefully addressed these points in the manuscript and respond to each comment below.

Major Points

1. Incomplete alignment between response letter and manuscript (Methods – tissue sampling)

The response letter states that hearts were collected from independent litters and that exclusion criteria were applied based on tissue quality. However, these details are not clearly and explicitly documented in the revised Methods section. Given the importance of litter effects and sample independence in developmental studies, I strongly recommend that the authors explicitly state: whether animals were derived from independent litters; whether multiple animals from the same litter were used; clearly defined inclusion/exclusion criteria at the sample level. At present, the manuscript does not fully reflect the level of detail described in the response.

Response:

We thank the reviewer for this important point and agree that these details should be stated explicitly in the Methods section rather than only in the response letter. We have therefore revised the Methods section to clarify sample origin and sample handling.

Specifically, we now clarify litter usage by stating that no more than two animals per litter were included per experimental group. We have also added explicit sample-level inclusion and exclusion criteria based on tissue and blot quality, including exclusion of samples or membranes with inadequate tissue integrity or uneven/insufficient transfer quality.

These revisions ensure alignment between the manuscript and the information provided in the response letter and improve transparency regarding sample independence and quality control.

2. Inconsistency in normalization strategy and loading controls. There appears to be a discrepancy between the Methods and the Results/figure legends regarding normalization. The Methods state that total protein staining was used only for quality control and that GAPDH/PKM were not used as normalization controls. However, in the Results/figure legends, GAPDH is still described as a loading control. This inconsistency is critical, particularly in a developmental context where housekeeping proteins may vary. The authors should:

- Clearly define the normalization strategy used for all quantified blots

- Ensure consistent reporting across Methods, Results, and figure legends

- Remove or revise any statements suggesting GAPDH-based normalization if it was not used

 

We thank the reviewer for identifying this inconsistency. We agree that the normalization strategy must be described clearly and consistently throughout the manuscript.

We have carefully revised the Methods, Results, and figure legends to ensure consistent reporting of the normalization approach. Specifically, we have removed residual wording that described GAPDH as a quantitative loading control where this was not the normalization basis used for densitometric analysis. We now state clearly that total protein staining was used to assess loading and transfer quality, while immunoblot quantification was interpreted as semi-quantitative developmental profiling under standardized loading conditions.

Where GAPDH or PKM blots are shown, these are now described consistently with their actual use in the study and no longer presented in a way that implies a contradictory normalization strategy. This revision was made throughout the manuscript to eliminate ambiguity.

 

3. Residual inconsistencies in statistical reporting. Although the Methods section has been updated to reflect one-way ANOVA with Tukey’s post hoc test, the Results section still contains references to Student’s t-test in some instances. This inconsistency raises concerns about whether all analyses were fully reprocessed.

The manuscript should be carefully checked to ensure:

A single, consistent statistical framework is described throughout

All legacy references to t-tests are removed if no longer applicable

Response:

We thank the reviewer for this careful observation. The reviewer is correct that references to Student’s t-test remained in the text. We confirm that all statistical analyses were consistently performed using pairwise Student’s t-tests for the analyses reported in the Results.

We would like to clarify that all statistical comparisons reported in the Results section are based exclusively on pairwise Student’s t-tests relative to the neonatal reference group, which represents the central biological comparator in this study. This approach was chosen to directly and transparently capture postnatal developmental changes with respect to a defined baseline (neonates), thereby preserving interpretability and graphical clarity.

We state that statistical significance relative to neonates best reflects the central aim of this study, namely the characterization of postnatal development using neonates as the reference group. In contrast, multiple interrelated comparisons across time points risk overinterpreting the postnatal trajectory and may render both the analysis and its graphical representation less transparent.

Including a full ANOVA framework would substantially broaden the scope of the analysis beyond the primary focus on developmental signaling addressed in this work. We therefore chose to retain a focused approach based on pairwise t-tests for the presentation of the Results, while using ANOVA only as a complementary, confirmatory analysis.

For completeness and transparency, we have included the corresponding ANOVA results in the Supplementary Material4. Uncropped Western blots not yet verifiable

- The authors indicate that uncropped full-length blots and membrane maps will be provided as supplementary material. However, in the current version available for review, these data are not included.

- Given the central role of Western blotting in this study, the inclusion of uncropped blots is essential for proper evaluation. These materials should be:

Included in the submission package

Clearly referenced in the manuscript

Organized in a way that allows direct comparison with the presented figures

Response:

We thank the reviewer for this careful observation. We agree with the reviewer that uncropped blots and membrane maps are important for proper evaluation of the immunoblot data. These materials have been prepared and are included as Supplementary Figures. The manuscript has been revised to clearly reference these supplementary figures alongside the corresponding main figures.

 

5. Evidence of incomplete editorial revision

The manuscript still contains several typographical issues, placeholder text (e.g., “[software, e.g., ImageJ]”), duplicated phrases, and fragmented sentences. While these do not invalidate the data, they reduce clarity and suggest that the revision process was not fully finalized. A careful editorial revision is needed to ensure:

Consistent and complete sentences

Removal of placeholders

Improved readability and professional presentation

Response:

We thank the reviewer for this comment and agree that the manuscript required a more careful final editorial revision. We have carefully revised the manuscript throughout to correct typographical and grammatical errors, remove placeholder text, eliminate duplicated or fragmented phrases, and improve overall clarity and consistency. We also reviewed figure legends, section cross-references, and methodological descriptions to ensure that the revised manuscript is complete and internally consistent.

Round 3

Reviewer 3 Report

Comments and Suggestions for Authors

The authors addressed all comments.