Review Reports

Round 1

Reviewer 1 Report

This manuscript by Yadav et al aims to explore the role of cysteine sulfenylation of DRP1 at C631 in macrophage reprogramming and neovascularization after ischemia. The study utilizes the novel approach of creating a “redox-dead” DRP1-C631A knock-in mouse model with the use of the CRISPR/Cas9 gene editing tool, followed by bone marrow transplant and hindlimb ischemia, to investigate the role of redox-dependent, non-canonical post-translational modifications of the mitochondrial fission machinery in macrophage reprogramming and neovascularization in the context of peripheral artery disease. The manuscript poses an important and timely question: does DRP1 sulfenylation play the role of a redox switch, integrating ischemic ROS production with reparative macrophage activity? The idea appears novel and has the potential to be impactful. However, there are certain methodological and conceptual issues with the manuscript, which are highlighted in the major and minor comments in my detailed comments.

 

Major comments

1. A major issue is that very small sample sizes undermine the reliability of critical results. Several in vitro tests (e.g., MitoTracker/MitoSOX in Figure 3, Seahorse OCR in Figure S3) were performed with sample sizes of n = 2, which is insufficient. It is suggested to increase the number of biological replicates to at least n = 3-5 for all tests, and the tests should be checked for the appropriate sample sizes used.

 

2. The bone marrow (BM) chimera strategy used by the authors does not allow myeloid-specific targeting. While the study aims to explore “myeloid DRP1 sulfenylation,” using a BM transplantation approach replaces all cells of the hematopoietic compartment, which include T cells, B cells, neutrophils, etc., with Drp1C/A cells. The phenotype in vivo therefore cannot be attributed to macrophages exclusively. The authors should use a myeloid cell-specific Cre-driven conditional knock-in strategy for Drp1 or provide data to rule out contributions from other hematopoietic cells.

 

3. The upstream ROS source of DRP1 sulfenylation has yet to be elucidated and is a primary concern for a ROS-specific journal like Antioxidants. Although this is recognized by the authors, they often cite NOX2 as the likely candidate based on prior work, without experimental evidence. Without experimental evidence, such as inhibition of NOX2 and the use of NOX2 knockout macrophages in the HSS model, this mechanistic model linking NOX2 to H2O2 to DRP1-CysOH is speculative and overemphasized in the discussion.

 

4. Lack of rescue or gain-of-function studies is another major issue. The study only employed the loss-of-function approach (C631A mutation). There is no demonstration of sufficiency using other approaches such as the sulfenylation mimetic mutation (for example, C631D), pharmacological enhancement of ROS, or overexpression of wild-type DRP1 in Drp1C/A macrophages. This weakens the support for the sufficiency of sulfenylation for the observed effects.

 

5. The metabolic characterization carried out by the authors is incomplete. In Drp1C/A BMDMs, the rate of extracellular acidification (ECAR), which is associated with glycolysis, is elevated, while the rate of oxygen consumption (OCR) is not altered. For OCR assays with Seahorse, n = 2 and no statistical analysis were performed (Figure S3). In addition, no direct analysis of TCA cycle intermediates such as succinate and itaconate or mitochondrial membrane potential was performed, despite their importance in macrophage polarization.

 

Minor comments:

1. The manuscript switches between human (Cys644) and mouse (Cys631) residue numbering without consistent clarification, which creates confusion (e.g., the discussion refers to a “DRP1-C644A KI mutation” that is actually a mouse model with a C631A mutation).

 

2. DCF-DA has poor specificity towards H2O2. Figure S2 uses DCF-DA to detect the production of H2O2, which is generally accepted to be nonspecific, detecting many ROS and being prone to false results. It would be better if the authors used more specific H2O2 sensors such as HyPer, roGFP2-Orp1 or even Amplex Red.

 

3. Typographical and formatting errors are scattered throughout the manuscript. There are many obvious errors, such as the use of double periods (page 7, section 3.2, line 4), the word "reprograming" instead of the correct word "reprogramming (page 3, Introduction, line 1)," and the word "statically" instead of the correct word "statistically" in the methods section (page 6, section 2.10, line 40).

 

4. The information about the gating strategy used in flow cytometry is not discussed in the manuscript. Although antibody and isotype controls are mentioned, a gating strategy is not shown in the main figures (2C to 2F). A complete gating strategy should be provided in supplementary information according to standard guidelines.

 

5. The age range of mice (8 to 15 weeks) is wide. An almost two-fold difference in age may lead to differences in immunologic responses and revascularization potential. It is recommended that the authors specify whether age is matched in WT and Drp1C/A groups or not.

 

6. While the introduction provides an proficient and logical overview of the work, it is still incomplete with regard to various aspects pertaining to the core content of this research. For example, there is insufficient introduction of protein sulfenylation biology, DRP1 post-translational modifications, and metabolic signaling pathways under investigation (AMPK and NF-κB). Extending these sections by three to four sentences will provide the reader with necessary background concepts without extending the paper excessively.

 

7. The references cited are generally relevant, yet the list appears to be of limited scope, with significant self-referencing and gaps in the literature on immunometabolism, sulfenylation biology, and DRP1 redox modifications as studied by others. Augmenting the list of references with 8 to 10 key references from other researchers would greatly add to the scholorly rigor and contextualization.

 

8. The current limitations section demonstrates selective transparency, acknowledging the conceptual limitations in such a way as to define the scope of future research, yet not discussing the methodological limitations, which could impact the current results. A balanced discussion of the limitations would include the conceptual limitations, which the authors handle well, and the limitations of the experimental design, which are not discussed at all.

 

Author Response

Please see the attachment for author's reply to the Reviewer1.

Author Response File: Author Response.docx

Reviewer 2 Report

This study provides compelling evidence that DRP1 cysteine sulfenylation at Cys631 acts as a redox switch linking ischemia-induced ROS to reparative macrophage polarization and revascularization. The work is innovative, mechanistically deep, and translationally relevant. However, several critical gaps and methodological weaknesses must be addressed before the conclusions can be fully endorsed.

1.The authors repeatedly invoke NOX2 as the likely upstream source based on prior work, but no direct evidence is provided in this manuscript. Without genetic or pharmacological blockade of NOX2 (or other ROS sources) in the HSS model, the claim that NOX2-derived ROS trigger DRP1-CysOH is merely correlative. 
2.Drp1C/A macrophages have reduced p-AMPK and increased p-NF-κB under HSS, but they do not test whether restoring AMPK activity (e.g., with AICAR) rescues the M2 phenotype or whether inhibiting NF-κB reverses M1 skewing.
3.The mitoSOX data show increased ROS in Drp1C/A macrophages, but the functional consequences of this increase are unexplored. Does it drive NF-κB activation? Is it sufficient to alter redox-sensitive transcription factors? Moreover, mitochondrial membrane potential or mtDNA release—key indicators of mitochondrial dysfunction—were not assessed. This limits the mechanistic insight into how mitoROS contributes to inflammation.
3.The Seahorse ECAR data show increased basal glycolysis and glycolytic capacity in Drp1C/A macrophages, but the authors do not link this to specific glycolytic enzymes or flux control. Is the increase due to enhanced glucose uptake, hexokinase activity, or PFKFB3? Without metabolic flux analysis or enzyme activity assays, the "glycolytic reprogramming" claim is circumstantial.
4.The increased neutrophil accumulation in Drp1C/A chimeras at day 3 is intriguing, but the authors do not test whether this is a cause or consequence of impaired efferocytosis. Given that efferocytosis is known to promote M2 polarization, the efferocytosis assays is neceessary to provide.
5.The DCP-Bio1 assay for sulfenylation is well-established, but the authors should include a negative control to confirm specificity.
6.Some figure labels are too small (e.g., Figure 2 contour plots), making it difficult to discern populations.

Author Response

Please see the attachment for author's reply to the reviewer 2.

Author Response File: Author Response.docx

Round 2

Reviewer 2 Report

The authors have addressed all my concerns.

None