Review Reports

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The manuscript addresses an important and timely topic. Bringing bioenergetic failure, cristae disruption, calcium imbalance, oxidative stress, and mitophagy into a common framework is an interesting approach. The sections on elamipretide, gene therapy, and mitochondrial genome editing are also useful. However, the central argument regarding mitochondrial quality control as a common “mechanistic hinge” appears somewhat stronger than the evidence currently available. Several points need further clarification.

1. The term “mechanistic hinge” may be too strong. Direct evidence is currently limited to a relatively small number of diseases and experimental models, and it remains unclear whether defective mitophagy is a necessary feature of all inherited mitochondrial cardiomyopathies.

2. Some of the supporting studies involve HFpEF, fatty-acid oxidation disorders, or other acquired cardiac conditions. These findings are relevant, but they should be clearly described as indirect evidence.

3. A summary table organized by disease or gene would be useful. It could include the primary mitochondrial defect, cardiac phenotype, evidence for altered mitophagy, and the experimental model used. Please also distinguish direct measurements of mitophagic flux from changes in related markers.

4. The contrast between mitochondrial and sarcomeric cardiomyopathies is drawn too sharply. Many nuclear mitochondrial disorders follow Mendelian inheritance, while sarcomeric cardiomyopathies can show incomplete penetrance and variable expression. This section should be reconsidered.

5. The definition of mitochondrial cardiomyopathy seems overly focused on persistent bioenergetic insufficiency. In some conditions, the initial defect involves mitochondrial dynamics, protein import, lipid remodeling, mtDNA maintenance, or proteostasis rather than simply reduced ATP production.

6. The statement that cardiomyocytes have “almost no bioenergetic reserve” is not entirely accurate. Limited ATP storage should not be equated with an absence of mitochondrial reserve capacity or metabolic flexibility.

7. The discussion places considerable emphasis on PINK1/Parkin. This may give the impression that it is the main mitophagy pathway in cardiomyocytes, whereas BNIP3-, NIX-, and FUNDC1-mediated pathways are also important. Basal cardiac mitophagy may also occur independently of Parkin. A more balanced discussion would be appropriate.

8. Mitophagy initiation is not equivalent to completed mitochondrial clearance. Changes in PINK1, Parkin, LC3-II, p62, or mitochondrial abundance alone are insufficient to demonstrate altered mitophagic flux. The role of lysosomal clearance should also be considered.

9. The discussion of cardiolipin, cristae curvature, and respiratory-chain supercomplexes is somewhat too definitive. Cardiolipin clearly contributes to inner-membrane organization, but the functional significance of supercomplex formation remains debated and may differ between experimental models. More cautious wording would be preferable.

10. The clinical interpretation of elamipretide needs greater precision. Forzinity received accelerated approval to improve muscle strength in patients with Barth syndrome weighing at least 30 kg, based primarily on knee-extensor strength rather than cardiac outcomes. It should not be presented as an established disease-modifying treatment for cardiomyopathy.

11. The therapeutic section would be easier to follow if evidence from cell studies, animal models, early clinical trials, and approved indications were discussed separately.

12. The section on heteroplasmy and tissue sampling needs clarification. Urinary epithelial cells or skeletal muscle may improve the detection of some mtDNA variants, but the heteroplasmy level in these tissues does not necessarily reflect the myocardial mutant load.

13. GDF15, FGF21, lactate, and circulating mtDNA are not cardiac-specific. They may be useful markers of systemic mitochondrial stress, but their value for monitoring mitochondrial cardiomyopathy should not be overstated.

14. The manuscript gives little information on how the literature was selected. Even for a narrative review, a brief description of the databases searched, search period, main terms, and selection approach would improve transparency.

Author Response

Response to Reviewer 1

Manuscript ID: ijms-4577021

Revised title: Mitochondrial Quality Control in Inherited Mitochondrial Cardiomyopathy: Convergent Pathobiology and a Testable Therapeutic Framework

Dear Reviewer,

Thank you for the careful review and specific suggestions. We have reconsidered the relationship between the central hypothesis and the evidence, added disease-specific studies, and revised the figures, tables, and therapeutic discussion. Our point-by-point responses follow. Locations refer to the revised manuscript; added or revised wording is shown in red, and Word comments identify the corresponding reviewer points.

For ease of reference, we have numbered your comments in their original order.

Comment 1

The term “mechanistic hinge” may be too strong. Direct evidence is currently limited to a relatively small number of diseases and experimental models, and it remains unclear whether defective mitophagy is a necessary feature of all inherited mitochondrial cardiomyopathies.

Response: We agree that the original wording treated the proposed mechanism too strongly. We have removed “mechanistic hinge” from the title and rewritten the abstract, central argument, and conclusion. The revised hypothesis is limited to selected genotypes and disease stages; impaired mitophagy is no longer described as necessary or sufficient for inherited mitochondrial cardiomyopathy. Section 4.4 now considers disease-specific supportive and discordant findings together, and Section 7 states outcomes that would challenge the hypothesis.

Location: Abstract (p. 1); Section 1 (p. 2); Section 4.4 (p. 9); Section 7 (p. 15); Section 8 (p. 18). Opening words: “Inherited mitochondrial cardiomyopathies arise from pathogenic variants affecting oxidative”.

Comment 2

Some of the supporting studies involve HFpEF, fatty-acid oxidation disorders, or other acquired cardiac conditions. These findings are relevant, but they should be clearly described as indirect evidence.

Response: We have labeled these findings as indirect evidence wherever they are used. The HFpEF, sarcomeric, ischemia–reperfusion, and fetal-hypoxia experiments are now presented as physiological or mechanistic comparisons. The CPT2 experiment is described as direct evidence within a fatty-acid oxidation-deficient mouse model, with indirect relevance to other mitochondrial genotypes. We have also clarified that the cited circulating-mtDNA study in Fabry disease concerns a lysosomal storage disorder. Table 2 identifies the comparator models separately.

Location: Section 2.1 (p. 4); Section 2.3 (p. 4); Section 4.4 (p. 10); Section 5 (p. 12); Table 2 (pp. 10–11). Opening words: “Experimental heart failure with preserved ejection fraction (HFpEF) and”.

Comment 3

A summary table organized by disease or gene would be useful. It could include the primary mitochondrial defect, cardiac phenotype, evidence for altered mitophagy, and the experimental model used. Please also distinguish direct measurements of mitophagic flux from changes in related markers.

Response: We have added Table 2, organized by disease or gene. It includes the primary defect, cardiac phenotype, experimental model, mitophagy-related observation, and the assay supporting that observation. The table distinguishes mitochondrial delivery to lysosomes, dynamic turnover evidence with its specificity limits, and static markers. It also identifies noncardiac models and areas where adequate cardiac flux evidence was not established. We do not classify a pH-sensitive reporter at a single time point as a complete degradation-rate measurement.

Location: Table 2 (pp. 10–11); Section 2.5 (p. 5). Opening words: “Initiation, lysosomal delivery, and completed degradation are different steps.”.

Comment 4

The contrast between mitochondrial and sarcomeric cardiomyopathies is drawn too sharply. Many nuclear mitochondrial disorders follow Mendelian inheritance, while sarcomeric cardiomyopathies can show incomplete penetrance and variable expression. This section should be reconsidered.

Response: We have removed the categorical contrast between mitochondrial and sarcomeric inheritance. The Introduction and Section 3 now state that nuclear mitochondrial disorders commonly follow Mendelian inheritance, while inherited mtDNA variants introduce maternal transmission and heteroplasmy and many large-scale deletions are sporadic. We also acknowledge incomplete and age-dependent penetrance and variable expression in sarcomeric cardiomyopathy, supported by a longitudinal study of sarcomere-variant carriers.

Location: Section 1 (p. 2); Section 3 (p. 7). Opening words: “Genetic architecture contributes to this variability without creating a”.

Comment 5

The definition of mitochondrial cardiomyopathy seems overly focused on persistent bioenergetic insufficiency. In some conditions, the initial defect involves mitochondrial dynamics, protein import, lipid remodeling, mtDNA maintenance, or proteostasis rather than simply reduced ATP production.

Response: We have broadened the definition to include primary inherited defects in OXPHOS, mtDNA maintenance, protein import, lipid remodeling, dynamics, and proteostasis. Persistent ATP insufficiency is no longer presented as the defining initiating event. The revised text also recognizes both cardiac-predominant and multisystem presentations. Table 1 and Section 2.4 now include protein surveillance and biogenesis as distinct parts of mitochondrial quality control.

Location: Section 1 (pp. 1–2); Section 2.4 (p. 5); Section 3.3 (p. 8); Table 1 (pp. 5–6). Opening words: “Inherited mitochondrial cardiomyopathy presents a clinical paradox: diverse genetic”.

Comment 6

The statement that cardiomyocytes have “almost no bioenergetic reserve” is not entirely accurate. Limited ATP storage should not be equated with an absence of mitochondrial reserve capacity or metabolic flexibility.

Response: This distinction is important, and we have corrected the statement. The text now separates small ATP stores from spare respiratory capacity and metabolic flexibility. We have also removed the claim that a genetically constrained heart has no residual flexibility. Related wording in the biomarker section and Table 3 has been corrected: PCr/ATP is described as an index of myocardial energetic state, not a direct measure of maximal respiratory reserve.

Location: Section 1 (p. 2); Section 2.1 (p. 4); Section 5 (p. 12); Table 3 (p. 12). Opening words: “The myocardium depends on continuous ATP production and has”.

Comment 7

The discussion places considerable emphasis on PINK1/Parkin. This may give the impression that it is the main mitophagy pathway in cardiomyocytes, whereas BNIP3-, NIX-, and FUNDC1-mediated pathways are also important. Basal cardiac mitophagy may also occur independently of Parkin. A more balanced discussion would be appropriate.

Response: We have rebalanced Section 2.5 and Table 1 to include BNIP3-, BNIP3L/NIX-, and FUNDC1-mediated pathways, as well as ULK1/RAB9-associated alternative mitophagy. Basal mitophagy independent of PINK1 is now discussed explicitly. The revised Figure 2 shows these inputs without assigning PINK1/Parkin universal dominance, and the proposed experiments consider receptor-mediated and lysosomal pathways in addition to the ubiquitin-linked route.

Location: Section 2.5 (p. 5); Table 1 (pp. 5–6); Figure 2 (p. 7); Section 7.1 (p. 17). Opening words: “Mitophagy is the selective lysosomal degradation of mitochondria and”.

Comment 8

Mitophagy initiation is not equivalent to completed mitochondrial clearance. Changes in PINK1, Parkin, LC3-II, p62, or mitochondrial abundance alone are insufficient to demonstrate altered mitophagic flux. The role of lysosomal clearance should also be considered.

Response: We have added a dedicated paragraph distinguishing initiation, lysosomal delivery, and completed degradation. Static protein abundance and mitochondrial mass are no longer treated as sufficient evidence of flux. We also explain that mt-Keima and mito-QC require interpretation in relation to time, lysosomal pH, and cargo persistence. Table 2 applies these distinctions to the cited disease studies, and Section 7.1 includes lysosomal acidification, proteolytic capacity, and complementary turnover measurements.

Location: Section 2.5 (p. 5); Table 2 (pp. 10–11); Section 7.1 (p. 17). Opening words: “Initiation, lysosomal delivery, and completed degradation are different steps.”.

Comment 9

The discussion of cardiolipin, cristae curvature, and respiratory-chain supercomplexes is somewhat too definitive. Cardiolipin clearly contributes to inner-membrane organization, but the functional significance of supercomplex formation remains debated and may differ between experimental models. More cautious wording would be preferable.

Response: We have qualified the discussion of cardiolipin, cristae geometry, and supercomplex function. The revised text retains cardiolipin’s established role in membrane organization but no longer states that supercomplex formation necessarily improves electron-transfer efficiency. We cite primary studies with differing conclusions about electron-flow organization and quinone channeling. Structural changes are now interpreted alongside functional measurements, and the Figure 2 legend makes the same limitation explicit.

Location: Section 2.2 (p. 4); Section 4.3 (p. 9); Figure 2 (p. 7). Opening words: “Cardiolipin contributes to inner mitochondrial membrane organization and interacts”.

Comment 10

The clinical interpretation of elamipretide needs greater precision. Forzinity received accelerated approval to improve muscle strength in patients with Barth syndrome weighing at least 30 kg, based primarily on knee-extensor strength rather than cardiac outcomes. It should not be presented as an established disease-modifying treatment for cardiomyopathy.

Response: We have checked the FDA labeling and made the indication consistent throughout. Forzinity received accelerated approval to improve muscle strength in adults and children with Barth syndrome weighing at least 30 kg, based on knee-extensor muscle strength as an intermediate clinical endpoint. We state the confirmatory requirement, the negative randomized primary endpoints, and the limitations of the open-label extension. The manuscript no longer presents approval as evidence of established cardiac disease modification or as a class-wide cardiomyopathy indication.

Location: Section 1 (p. 2); Section 6.1 (p. 13); Table 4 (p. 15); Section 8 (p. 18). Opening words: “Therapeutic progress makes this mechanistic question clinically relevant. Elamipretide”.

Comment 11

The therapeutic section would be easier to follow if evidence from cell studies, animal models, early clinical trials, and approved indications were discussed separately.

Response: We have reorganized the therapeutic discussion using explicit evidence-stage labels. Cellular and animal findings, early human studies, and approved indications are now presented separately, and Table 4 uses distinct columns for preclinical and human evidence. The revision also includes the 2026 early AAV-FXN clinical report, while retaining its nonrandomized design, exploratory outcomes, and safety limitations. Genetic Usp30 deletion is no longer described as demonstrated pharmacological efficacy.

Location: Section 6 (p. 13); Section 6.1 (p. 13); Section 6.2 (p. 13); Section 6.3 (p. 14); Table 4 (p. 15). Opening words: “Supportive heart-failure, conduction, and arrhythmia management remains essential and”.

Comment 12

The section on heteroplasmy and tissue sampling needs clarification. Urinary epithelial cells or skeletal muscle may improve the detection of some mtDNA variants, but the heteroplasmy level in these tissues does not necessarily reflect the myocardial mutant load.

Response: We have clarified that urine epithelial cells or skeletal muscle can improve detection of selected mtDNA variants, depending on the variant, age, and tissue distribution. Their heteroplasmy levels are not presented as estimates of myocardial mutant load. The revised paragraph states this distinction directly and emphasizes clinical cardiac assessment, imaging, and rhythm surveillance for risk evaluation.

Location: Section 3.1 (p. 8). Opening words: “Pathogenic mtDNA variants associated with cardiomyopathy occur in protein-coding”.

Comment 13

GDF15, FGF21, lactate, and circulating mtDNA are not cardiac-specific. They may be useful markers of systemic mitochondrial stress, but their value for monitoring mitochondrial cardiomyopathy should not be overstated.

Response: We have narrowed their proposed roles to systemic diagnostic support or exploratory longitudinal assessment. GDF-15, FGF-21, lactate, and circulating mtDNA are not described as cardiac-specific markers or validated surrogates for myocardial mitophagy or clinical benefit. Section 5 and Table 3 now distinguish these measures from cardiac imaging, rhythm assessment, and conventional cardiac biomarkers. Section 7.3 also explains that patient-derived cell phenotypes are not validated measures of turnover in the living myocardium.

Location: Section 5 (pp. 12–13); Table 3 (p. 12); Section 7.3 (p. 17). Opening words: “Lactate is affected by collection technique, exertion, perfusion, hepatic”.

Comment 14

The manuscript gives little information on how the literature was selected. Even for a narrative review, a brief description of the databases searched, search period, main terms, and selection approach would improve transparency.

Response: We have added Section 1.1 describing the targeted search undertaken for this revision: PubMed/MEDLINE through 12 September 2026 without a lower date limit, the principal search concepts, reference-list review, selected full-text assessment, and consultation of FDA and ClinicalTrials.gov sources. We state the preference for disease-specific primary cardiac studies and the inclusion of contradictory findings. The section identifies the article as a narrative review and states that exhaustive retrieval and formal risk-of-bias assessment were not undertaken.

Location: Section 1.1 (p. 3). Opening words: “This is a critical narrative review, not a systematic”.

Sincerely,
Chung-Lin Lee
On behalf of all authors

 

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

The manuscript by Chung-Lin Lee and co-authors is a review article on the impact of mitochondrial quality control in mitochondrial cardiomyopathies. The authors propose that this serves as a mechanistic hinge for multiple disorders with convergent pathobiology and propose a stratified mechanism-guided route towards targeted therapy. This is an interesting article but would benefit from several clarifications, modifications and revisions.

Comments:

1) The introduction seems rather generic and would benefit from substantial revisions in order to make it more focused, conveying key points and information to the reader. For example, it should clearly state and address the clinical paradox of mitochondrial cardiomyopathies, the mechanistic problem and therapeutic options. The author’s hypothesis should then be explained along with the main aim of the review.

2) The manuscript cites a total of 46 references, which is a particularly low number for a review article. Importantly, there are numerous instances where several sentences or even paragraphs do not contain any citation. This is of major concern and is unacceptable practice in scientific writing.   

3) The genetic variant of CHCHD10 is mentioned in line 205, however, the functional role of this protein is not explained.

4) In its current form, Figure 1 does not appear to accurately depict the main concept of the mechanistic hinge. The mitophagy box should be placed beneath the mechanistic nodes so that all disease pathways should convene through impaired mitophagy.

5) Figure 2 is rather simplistic. Also, since membrane architecture is referring to IMM then the arrow should point to the inner membrane.

6) Line 275: Their cardiac risk is often electrical, please rephrase.

7) In Table 3, AAV-FXN strategy is associated with systemic AAV toxicity. Is AAV-toxicity not a critical limitation in the case of AAV-TAZ?

8) Given that elamipretide and AAV-TAZ influence cardiolipin and since they have both been evaluated as therapeutic strategies in Barth syndrome, which avenue do the author envision would be the most promising?  

9) A schematic figure on the central hypothesis and the three predictions that are outlined in section 7 would be helpful.

10) The three stages of section 7 appear as the author’s suggestions on how to address the three predictions. This does not exclude the fact that there may be additional factors or avenues that could be explored towards this and this should clearly be stated. For example, regarding stage 1 it is unclear why this is focused only on iPSC-cardiomyocyte experiment and does not assess mitochondrial flux in relevant animal models. In addition, while Table 1 lists several key effectors that are participating in mitochondrial quality control machinery it is unclear why stage 1 is focused only on TAZ and FXN.

11) The conclusion and outlook section appears as a reiteration of the main points of the manuscript, with the outlook part being limited to the last 5 lines of the manuscript.    

12) There are statements and conclusions that are stronger than the provided evidence. For example, mitochondrial dysfunction does not automatically establish convergence on defective mitophagy. In addition, the author’s hypothesis is still not validated and therefore should be treated as a hypothesis.  

13) The manuscript should clearly distinguish mitochondrial quality control from mitophagy, which tend to be used interchangeable. Mitophagy is one component of quality control, and the authors should explain why it is so centrally placed in their hypothesis. This is particularly required since the title mentions mitochondrial quality control as the mechanistic hinge.

14) It would be useful to clarify that the term mitochondrial cardiomyopathy refers to multisystem mitochondrial disorders with cardiac involvement. Along those lines, given the multisystem pathophysiology of patients with Barth syndrome and Friedreich ataxia, the two conditions which are extensively used as examples in the manuscript, how do the authors envision that this could affect choice and effectiveness of therapeutic strategies?

15) Mitophagy failure as the mechanistic hinge is based on evidence from one reference (26) in fatty-acid oxidation-deficient mouse hearts. This appears particularly weak, especially given that this concept is a central node of the author’s hypothesis. In addition, this concept is then extrapolated in other conditions such as Barth syndrome and Friedreich ataxia without sufficient experimental evidence to support this.     

16) The therapeutic potential of mitophagy modulation is similarly weak, as again it is only based on one reference (again reference 26).  

Author Response

Response to Reviewer 2

Manuscript ID: ijms-4577021

Revised title: Mitochondrial Quality Control in Inherited Mitochondrial Cardiomyopathy: Convergent Pathobiology and a Testable Therapeutic Framework

Dear Reviewer,

Thank you for the careful review and specific suggestions. We have reconsidered the relationship between the central hypothesis and the evidence, added disease-specific studies, and revised the figures, tables, and therapeutic discussion. Our point-by-point responses follow. Locations refer to the revised manuscript; added or revised wording is shown in red, and Word comments identify the corresponding reviewer points.

Comment 1

The introduction seems rather generic and would benefit from substantial revisions in order to make it more focused, conveying key points and information to the reader. For example, it should clearly state and address the clinical paradox of mitochondrial cardiomyopathies, the mechanistic problem and therapeutic options. The author’s hypothesis should then be explained along with the main aim of the review.

Response: We have substantially rewritten the Introduction around the clinical paradox of overlapping phenotypes but variable progression. It now defines the disease spectrum, explains why ATP supply alone does not capture all primary defects, and identifies the unresolved mechanistic question. Current therapeutic opportunities and their limits then lead to the explicitly stated hypothesis and the aim of the review. We have also removed several categorical statements that were not supported across genotypes.

Location: Section 1 (pp. 1–3). Opening words: “Inherited mitochondrial cardiomyopathy presents a clinical paradox: diverse genetic”.

Comment 2

The manuscript cites a total of 46 references, which is a particularly low number for a review article. Importantly, there are numerous instances where several sentences or even paragraphs do not contain any citation. This is of major concern and is unacceptable practice in scientific writing.

Response: We have reviewed the citation coverage throughout the manuscript and expanded the reference list from 46 to 78 sources. Added references address disease-specific mitophagy evidence, conflicting findings, assay interpretation, alternative quality-control pathways, supercomplex biology, tissue heteroplasmy, AAV safety, and the 2026 human AAV-FXN report. Assertions previously lacking support have been cited, qualified, or removed. We have also checked bibliographic details and renumbered the references in order of first citation, including the tables.

Location: Section 1.1 (p. 3); Section 4.4 (p. 9); Table 2 (pp. 10–11); Section 6.2 (p. 13); References (pp. 20–24). Opening words: “This is a critical narrative review, not a systematic”.

Comment 3

The genetic variant of CHCHD10 is mentioned in line 205, however, the functional role of this protein is not explained.

Response: We have added the function of CHCHD10 before discussing the variant. It is described as an intermembrane-space protein involved in mitochondrial proteostasis and cristae maintenance, with disease-associated aggregation and OMA1–DELE1–HRI stress signaling in the knock-in model. We also distinguish the mouse p.S55L variant from the corresponding human p.S59L variant and clarify that the cited experiments do not establish mitophagy as the mediator of the cardiac phenotype.

Location: Section 2.4 (p. 5). Opening words: “CHCHD10 is an intermembrane-space protein involved in mitochondrial proteostasis”.

Comment 4

In its current form, Figure 1 does not appear to accurately depict the main concept of the mechanistic hinge. The mitophagy box should be placed beneath the mechanistic nodes so that all disease pathways should convene through impaired mitophagy.

Response: We have redrawn Figure 1 with the mitophagy–lysosome module below the interacting mechanistic nodes, as suggested. We have used dashed convergence arrows because the revised hypothesis is not established in every disease, and we retained a separate route from mitochondrial injury to cardiac outcomes. Routing every disease pathway through impaired mitophagy would imply a requirement that the present evidence cannot establish. The figure and legend now make this distinction explicit.

Location: Figure 1 (p. 3); Section 1 (p. 2). Opening words: “We examine whether failure to match mitochondrial damage with”.

Comment 5

Figure 2 is rather simplistic. Also, since membrane architecture is referring to IMM then the arrow should point to the inner membrane.

Response: Figure 2 has been redrawn with labeled outer membrane, inner membrane, intermembrane space, and matrix. The membrane-architecture arrow now ends on an inner-membrane crista. Respiratory complexes and ATP synthase are placed on the inner membrane, and the lower panel distinguishes broader quality-control functions from mitophagy. Recognition, sequestration, lysosomal delivery, and degradation are shown as separate steps.

Location: Figure 2 (p. 7); Section 2.5 (p. 5). Opening words: “Initiation, lysosomal delivery, and completed degradation are different steps.”.

Comment 6

Line 275: Their cardiac risk is often electrical, please rephrase.

Response: We have replaced the sentence with a more precise description: “Progressive atrioventricular block and His–Purkinje conduction disease may precede overt ventricular dysfunction and can lead to sudden death.” The following sentences explain why rhythm surveillance is required even when ejection fraction is preserved.

Location: Section 3.1 (p. 8). Opening words: “Single large-scale mtDNA deletions can cause the Pearson–Kearns–Sayre spectrum.”.

Comment 7

In Table 3, AAV-FXN strategy is associated with systemic AAV toxicity. Is AAV-toxicity not a critical limitation in the case of AAV-TAZ?

Response: Yes. The original table was inconsistent on this point. We now list systemic AAV immune, hepatic, and complement-associated risks for both AAV-TAZ and AAV-FXN in Section 6.2 and Table 4 (formerly Table 3). We distinguish these shared platform risks from the additional risk of excessive frataxin expression. We do not imply that the frequency or severity of toxicity is identical between vectors or products.

Location: Section 6.2 (pp. 13–14); Table 4 (p. 15). Opening words: “Safety considerations shared by AAV strategies. Systemic vector delivery”.

Comment 8

Given that elamipretide and AAV-TAZ influence cardiolipin and since they have both been evaluated as therapeutic strategies in Barth syndrome, which avenue do the author envision would be the most promising?

Response: We have added a direct comparison in Section 6.4. Elamipretide has the nearer-term clinical advantage of an approved muscle-strength indication in eligible patients. AAV-TAZ has the stronger etiologic rationale and encouraging mouse cardiac results, but requires clinical validation and carries gene-delivery risks. We cannot currently rank their ability to prevent or reverse cardiomyopathy because there is no head-to-head evidence and their evidence stages differ. Possible complementary or sequential use is identified as untested, rather than recommended.

Location: Section 6.4 (p. 14); Section 6.1 (p. 13); Section 6.2 (pp. 13–14). Opening words: “For Barth syndrome, elamipretide has the nearer-term clinical advantage”.

Comment 9

A schematic figure on the central hypothesis and the three predictions that are outlined in section 7 would be helpful.

Response: We have added Figure 3. It presents the bounded central hypothesis and the three predictions concerning progression, selective rescue, and disease stage. Each prediction is paired with the measurements required and a result that would weaken it. The figure also identifies human-cell, animal, and clinical studies as complementary approaches rather than a single compulsory sequence.

Location: Section 7 (pp. 15–16); Figure 3 (p. 16). Opening words: “We propose that, in a subset of inherited mitochondrial”.

Comment 10

The three stages of section 7 appear as the author’s suggestions on how to address the three predictions. This does not exclude the fact that there may be additional factors or avenues that could be explored towards this and this should clearly be stated. For example, regarding stage 1 it is unclear why this is focused only on iPSC-cardiomyocyte experiment and does not assess mitochondrial flux in relevant animal models. In addition, while Table 1 lists several key effectors that are participating in mitochondrial quality control machinery it is unclear why stage 1 is focused only on TAZ and FXN.

Response: We have revised Stage 1 to include in vivo reporter studies and isolated adult cardiomyocytes alongside isogenic iPSC-derived and engineered cardiac models. Model selection now spans lipid remodeling, iron–sulfur biology, OXPHOS assembly, import, translation, mtDNA, and dynamics/proteostasis, with illustrative genes including TAFAZZIN, FXN, ACAD9, AGK, FARS2, and CHCHD10. The pathway perturbations also extend beyond PINK1/Parkin. The final paragraph of Section 7 explicitly states that the stages are neither exhaustive nor mandatory and describes additional multicellular, spatial, import, and proteostasis approaches.

Location: Section 7.1 (p. 17); Section 7.2 (p. 17); Section 7.3 (p. 17); Figure 3 (p. 16). Opening words: “Stage 1 should use complementary human and animal systems”.

Comment 11

The conclusion and outlook section appears as a reiteration of the main points of the manuscript, with the outlook part being limited to the last 5 lines of the manuscript.

Response: We have shortened the recap and rewritten the outlook around specific unresolved questions: identifying the relevant subgroup, standardizing delivery-versus-degradation assays, testing selective causal rescue, and linking target engagement to cardiac and extracardiac outcomes. The conclusion now discusses how negative findings or alternative mechanisms would redirect the framework, and it avoids presenting an unvalidated fibrosis threshold or a universal quality-control mechanism as established.

Location: Section 8 (p. 18). Opening words: “Inherited mitochondrial cardiomyopathies share several forms of cellular stress,”.

Comment 12

There are statements and conclusions that are stronger than the provided evidence. For example, mitochondrial dysfunction does not automatically establish convergence on defective mitophagy. In addition, the author’s hypothesis is still not validated and therefore should be treated as a hypothesis.

Response: We have revised these statements throughout, including the title and abstract. Mitochondrial dysfunction is no longer treated as proof of impaired mitophagy, and the hypothesis is explicitly restricted to selected genotypes and stages. Section 4.4 includes discordant observations, Figure 1 retains alternative injury routes, and Section 7 specifies informative negative results. The proposed fibrosis effect is also now a hypothesis about treatment response, not a known irreversible threshold.

Location: Abstract (p. 1); Section 1 (p. 2); Section 4 (p. 9); Section 4.4 (p. 10); Section 7 (p. 15); Section 8 (p. 18). Opening words: “Inherited mitochondrial cardiomyopathies arise from pathogenic variants affecting oxidative”.

Comment 13

The manuscript should clearly distinguish mitochondrial quality control from mitophagy, which tend to be used interchangeable. Mitophagy is one component of quality control, and the authors should explain why it is so centrally placed in their hypothesis. This is particularly required since the title mentions mitochondrial quality control as the mechanistic hinge.

Response: We have defined mitochondrial quality control as the broader system of protein surveillance, membrane maintenance, dynamics, biogenesis, and disposal. Mitophagy is consistently described as one component. Its focus in this review is justified by its connection between mitochondrial injury and lysosomal disposal and the availability of experimental measurements and perturbations; this focus is not presented as evidence of universal mechanistic dominance. Table 1, Figure 2, and the experimental framework have been revised accordingly.

Location: Section 1 (p. 2); Section 2.4 (p. 5); Section 2.5 (p. 5); Table 1 (pp. 5–6); Figure 2 (p. 7); Section 7 (p. 15). Opening words: “We examine whether failure to match mitochondrial damage with”.

Comment 14

It would be useful to clarify that the term mitochondrial cardiomyopathy refers to multisystem mitochondrial disorders with cardiac involvement. Along those lines, given the multisystem pathophysiology of patients with Barth syndrome and Friedreich ataxia, the two conditions which are extensively used as examples in the manuscript, how do the authors envision that this could affect choice and effectiveness of therapeutic strategies?

Response: We have clarified that mitochondrial cardiomyopathy commonly occurs within a multisystem disorder, while retaining recognized cardiac-predominant presentations. New Section 6.4 addresses how skeletal myopathy, neutropenia, growth, neurological disability, diabetes, and organ-specific exposure may affect eligibility, safety, and treatment benefit. It also explains why better walking performance or lower systemic stress markers cannot alone establish cardiac efficacy. Heart-directed gene delivery is not assumed to treat neurological disease, and the proposed clinical studies now separate cardiac from extracardiac outcomes.

Location: Section 1 (pp. 1–2); Section 6.4 (pp. 14–15); Section 5 (p. 13); Section 7.3 (p. 17). Opening words: “Inherited mitochondrial cardiomyopathy presents a clinical paradox: diverse genetic”.

Comment 15

Mitophagy failure as the mechanistic hinge is based on evidence from one reference (26) in fatty-acid oxidation-deficient mouse hearts. This appears particularly weak, especially given that this concept is a central node of the author’s hypothesis. In addition, this concept is then extrapolated in other conditions such as Barth syndrome and Friedreich ataxia without sufficient experimental evidence to support this.

Response: We agree that one fatty-acid oxidation model was insufficient support for the original broad claim. We have added disease-specific studies in Barth syndrome, frataxin deficiency, and FARS2-related models, and assessed their assay limitations in the new Table 2. Importantly, the revision includes increased-clearance or context-dependent findings rather than selecting only supportive studies. The CPT2 study remains a model-specific mechanistic experiment. We have therefore narrowed the central claim rather than presenting the added references as proof of a universal hinge.

Location: Section 4.4 (pp. 9–10); Table 2 (pp. 10–11); Section 7 (p. 15). Opening words: “Barth syndrome provides disease-specific support, with important assay limitations.”.

Comment 16

The therapeutic potential of mitophagy modulation is similarly weak, as again it is only based on one reference (again reference 26).

Response: We have revised this section to distinguish proof of concept from a treatment ready for clinical use. The discussion now includes the disease-specific Barth rapamycin experiment and the broader network interventions in FARS2 models, while acknowledging pleiotropy and the possibility that the appropriate intervention may reduce excessive removal rather than increase it. There is no claim of established clinical efficacy for selective mitophagy modulation. Section 7 further requires verified correction of turnover, preserved respiratory mass, cardiac benefit, and pathway-specific tests before attributing rescue to mitophagy.

Location: Section 6.3 (p. 14); Table 4 (p. 15); Section 7 (p. 16). Opening words: “Preclinical mitophagy-directed interventions. Usp30 deletion in CPT2-deficient hearts provides”.

Sincerely,
Chung-Lin Lee
On behalf of all authors

Author Response File: Author Response.pdf

Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

Thank you for the detailed point-to-point respose, for addressing my comments and revising the manuscript accordingly. Ths has led to its significant improvement and it can now be accepted for publication.