Enzymatic/Mitochondrial Import Bottleneck in Sepsis with Possible Extensions to DIC: IV Glutathione and Hinokitiol as Potential Therapeutic Candidates

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The central hypothesis is interesting but there are principal methodological flaws in the manuscript. I recommend complete re-analysis and re-submission, not an ordinary major revision. Here are the reasons:
1. The study does not actually analyze sepsis-induced DIC. The transcriptomic datasets compare sepsis/septic shock with healthy controls, but authors nevertheless repeatedly describe the transcriptomic signatures as mechanisms of "sepsis-associated DIC". Therefore the present data can, at most, support a hypothesis about the GSH axis in sepsis, not a mechanism of sepsis-associated DIC.
2. There are major errors in the identification and description of the GEO datasets. This is particularly concerning because the manuscript is largely computational.
GSE13904 is described as a Cazalis et al. cohort containing 158 adult septic patients. However, GSE13904 is actually the Wong et al. pediatric SIRS/sepsis/septic-shock cohort https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc=GSE13904 
GSE54514 is described as 127 septic-shock patients plus 36 controls. The official GEO record instead describes 35 septic patients: 26 survivors / 9 nonsurvivors / 18 healthy at different time points https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc=GSE54514 Thus, 127 septic arrays are not 127 independent patients. Treating longitudinal samples as independent observations produces pseudoreplication and artificially small P values.
The description of GSE46955 as LC-MS/MS proteomics is incorrect. It is indeed transciptomics using the Illumina HumanRef-8 v2.0 expression beadchip. So all the claims about "protein-level validation" are wrong.
3. Some other flaws: xCell analysis cannot establish "cell-intrinsic suppression"; expression of NLRP3 and GSDMD is being confused with activation of the NLRP3/GSDMD pathway; GCLC/GCLM mRNA doesn’t measure GCL enzymatic activity.

Author Response

Dear Respected Reviewer 1,

We sincerely thank you for your rigorous evaluation of our manuscript. Your assessment identified critical methodological and descriptive errors, and we have taken your recommendation for a complete re-analysis seriously. The response below reflects a substantive re-analysis of the underlying data. We greatly appreciate the time and effort directed toward providing this constructive feedback. Point-by-point responses are provided below, with manuscript revisions highlighted in red and accompanied by corresponding line numbers.

General comment

The central hypothesis is interesting but there are principal methodological flaws in the manuscript. I recommend complete re-analysis and re-submission, not an ordinary major revision.

We thank the Reviewer for this direct assessment. In response, we undertook a full re-analysis of the GSE54514 cohort at both the bulk and cell-type level, corrected all three dataset-identification errors described below against the primary GEO records, and revised the manuscript's language throughout to distinguish transcript-level findings from the pathway- and enzyme-activity-level claims the original text implied. We address each specific point in turn.

1. The study does not analyze sepsis-induced DIC

"The study does not actually analyze sepsis-induced DIC. The transcriptomic datasets compare sepsis/septic shock with healthy controls, but authors nevertheless repeatedly describe the transcriptomic signatures as mechanisms of “sepsis-associated DIC. Therefore the present data can, at most, support a hypothesis about the GSH axis in sepsis, not a mechanism of sepsis-associated DIC."

We thank the Reviewer for this important observation, which is correct: none of the four GEO cohorts stratify patients by DIC status, ISTH score, or coagulation parameters. We have revised the Abstract, Introduction, Results, and Conclusions throughout to state explicitly that the bioinformatic findings support a hypothesis about glutathione-axis dysfunction in sepsis broadly, and that extending this axis to a specific mechanistic role in DIC rests on the independent mechanistic literature discussed in Section 3, not on the transcriptomic data generated here, furethermore, we also made the drastic decision to change the title of the manuscript to “The enzymatic/mitochondrial import bottleneck in Sepsis with possible extensions to DIC : IV Glutathione and Hinokiotiol as potential therapeutic candidates”.

 A new Limitations subsection (3.8.6) makes this scope explicit. The revised Abstract now reads:

"These findings, derived from sepsis-versus-control cohorts without DIC adjudication, establish that myeloid GSH synthesis and mitochondrial import failure co-localise with NLRP3/GSDMD transcript upregulation in sepsis. Extending this axis to a mechanistic role in DIC is a hypothesis supported by independent literature, not a direct finding of the present dataset." [lines 35-39 ; 904-911]

 We consider this an appropriate and necessary recalibration, since the DIC linkage remains available as a well-supported hypothesis for a future, DIC-stratified study (Section 3.9).

2. Errors in dataset identification and description

We verified each of the following directly against the primary GEO records before revising, given the Reviewer's correct observation that this is especially consequential in a largely computational manuscript.

2A. GSE13904 mislabeled as an adult cohort

"GSE13904 is described as a Cazalis et al. cohort containing 158 adult septic patients. However, GSE13904 is actually the Wong et al. pediatric SIRS/sepsis/septic-shock cohort."

We thank the Reviewer for identifying this error. We confirm that GSE13904 is the pediatric SIRS/sepsis/septic-shock cohort published by Wong et al. We have corrected the attribution and demographic descriptions throughout the manuscript (Abstract, Section 4.1, Table 5). Additionally, we have added the following statement to the Limitations section acknowledging age heterogeneity:

"GSE13904 (Wong et al.) profiles a pediatric SIRS/sepsis/septic-shock cohort, whereas GSE54514 and GSE28750 profile adult populations. This age heterogeneity limits cross-dataset generalisability; consequently, cross-platform directional consistency, rather than pooled effect size, is emphasised throughout this study." [lines 931-934]

 

2B. GSE54514 patient counts and pseudoreplication

"GSE54514 is described as 127 septic-shock patients plus 36 controls. The official GEO record instead describes 35 septic patients: 26 survivors / 9 nonsurvivors / 18 healthy at different time points. Thus, 127 septic arrays are not 127 independent patients. Treating longitudinal samples as independent observations produces pseudoreplication and artificially small P values."

We thank the Reviewer for identifying this methodological failure point, which prompted the most substantial revision in this response. We confirm GSE54514 comprises 35 septic patients (26 survivors, 9 non-survivors) and 18 healthy controls, sampled longitudinally for up to five days. In verifying this, we additionally identified a data-quality defect in the deposited GEO metadata itself: one sample (GSM1317938, labeled “sepsis_nonsurvivor, Day_4, ID=20”) does not correspond to any patient present at Day 1, 2, 3, or 5, and was inflating our own patient count from 35 to 36. This sample has been excluded, and the full pipeline re-run on the corrected 162-array dataset.

We addressed the pseudoreplication concern with two distinct, purpose-matched analyses:

 

For the bulk, condition-level comparison we retained all 162 longitudinal arrays and fitted a linear mixed-effects model with day as a fixed covariate and a random intercept per patient, which explicitly models the repeated-measures structure the Reviewer identifies. This is reported in a new Table 1, alongside the intraclass correlation and BH-adjusted significance for both the main condition effect and the condition-by-day interaction.

“Of the eight genes modelled, only NLRP3 and FUNDC1 showed a condition-by-day interaction reaching nominal significance (uncorrected p < 0.05); neither survived Benjamini–Hochberg correction and both are reported as exploratory. … Because GSE54514's septic cohort loses non-survivors over the sampling window, later timepoints are increasingly weighted toward survivors; a declining NLRP3 trajectory is therefore also consistent with informative dropout rather than a true within-patient resolution of inflammasome transcription, and the present model cannot distinguish between these explanations.” [lines 123-134]

For the cell-type deconvolution analysis we deliberately did not extend the mixed-effects framework to the xCell-derived scores. Modelling repeated-measures structure directly on top of an already-estimated, compositionally-derived score introduces its own unresolved assumptions. xCell enrichment itself is not a stable per-patient trait sampled repeatedly, but a marker of a physiological state that is expected to change as sepsis evolves, so a “patient random effect” on top of it does not have a clean interpretation. We therefore restricted the deconvolution analysis to one sample per patient (Day 1), yielding an independent sample of 53 patients (35 sepsis, 18 control) with no repeated-measures structure to correct for by design, and computed Spearman correlations on this subset.

2C. GSE46955 misdescribed as LC-MS/MS proteomics

"The description of GSE46955 as LC-MS/MS proteomics is incorrect. It is indeed transcriptomics using the Illumina HumanRef-8 v2.0 expression beadchip. So all the claims about “protein-level validation” are wrong."

We thank the Reviewer for catching this. GSE46955 was generated using the Illumina HumanRef-8 v2.0 expression beadchip (GPL6104), an mRNA microarray. We have corrected this throughout (Methods 4.2, Table 4a's caption, and the Conclusions) and removed all claims that this cohort provided protein-level validation. The corrected Methods text now reads:

“GSE46955, generated by Shalova et al. using the Illumina HumanRef-8 v2.0 expression beadchip (GPL6104) on isolated peripheral blood monocytes … provided the only available dataset combining cell-type specificity, temporal resolution, and transcript-level quantification in the same individuals.” [lines 1022-1028]

3. Overclaiming from the computational methods

xCell analysis cannot establish “cell-intrinsic suppression”; expression of NLRP3 and GSDMD is being confused with activation of the NLRP3/GSDMD pathway; GCLC/GCLM mRNA doesn’t measure GCL enzymatic activity.

We agree with each of these three points. xCell provides a computational estimate of cell-type composition, not single-cell ground truth. Furthermore, transcript-level upregulation does not equate to inflammasome assembly, and transcript abundance does not reflect holoenzyme assembly or catalytic activity. We have revised the Results section to describe transcript-level associations strictly. Terms implying "cell-intrinsic suppression" or pathway "activation" have been removed, reserving activation-level terminology solely for instances where we cite literature detailing post-translational events. Three corresponding Limitations subsections have been added to state these constraints explicitly

Summary

We believe this response reflects the complete re-analysis the Reviewer requested. This revision reflects a complete re-analysis of the data. We have corrected three dataset-identification errors against primary sources, removed a previously unrecognized data-quality defect, resolved pseudoreplication using appropriate statistical frameworks, and recalibrated the manuscript's language to accurately reflect transcript-level evidence. We thank the Reviewer again for an assessment that has fundamentally improved the rigor of this work. 

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

The manuscript demonstrates a substantial body of work, a profound understanding of the underlying mechanisms, and a highly creative attempt to integrate mitochondrial redox biology, inflammasome activation, and endothelial dysfunction into a unified model of sepsis-associated disseminated intravascular coagulation (DIC). The cross-dataset deconvolution analysis is a major highlight, and the finding regarding the coordinated inhibition of the GCLC–SLC25A39–NLRP3 axis in myeloid cells is compelling. However, the manuscript is overly long, with some sections reading more like an exhaustive review than an analysis grounded in the study's results. While the core hypothesis is intriguing, current inferences extend beyond what the existing data support; the narrative would be more coherent if there were a clearer distinction between direct findings (e.g., "GCLC inhibition in monocytes") and mechanistic inferences drawn from external literature (e.g., "this should trigger endothelial apoptosis and DIC"). It is recommended to streamline the discussion, eliminate redundancies, and include a schematic diagram to aid reader comprehension of this multi-step model. Most importantly, study limitations should be articulated more clearly, and definitive therapeutic claims—such as those regarding the efficacy of intravenous glutathione combined with honokiol—should be avoided in the absence of experimental validation. With substantial restructuring, this work has the potential to become a robust and thought-provoking study.

Author Response

Dear Respected Reviewer 2,

We sincerely thank you for your generous and constructive assessment of our manuscript, and in particular for recognizing the cross-dataset deconvolution analysis and the GCLC–SLC25A39–NLRP3 finding as the core contribution of this work. Your comments correctly identified discrepancies in the original submission between the strength of our direct results and the length and confidence with which we extrapolated beyond them. We have undertaken a substantial revision in response to your feedback. Responses are provided below, with manuscript revisions highlighted in red.

1. Manuscript length and review-like sections

"The manuscript is overly long, with some sections reading more like an exhaustive review than an analysis grounded in the study's results”

We completely agree with the reviewer, section 3.2 ("Converging Pathways to DIC"), the mechanistic discussion linking GCL failure to endothelial apoptosis, pyroptosis, and NK cell dysfunction, was the principal contributor to this problem. It previously narrated multiple external studies at full methodological detail (assay technique, exact quantitative results, model system). We have aggressively condensed this section by approximately 35%, retaining the complete logical chain while removing methods-level detail that belongs in the cited papers rather than our Discussion.

An important note on overall length: We must transparently note that while we heavily streamlined the sections, addressing the critical methodological and analytical requirements raised by the other reviewers unfortunately necessitated adding substantial new explanatory text elsewhere. Consequently, while the narrative is now significantly more mainstream, focused, and accessible as per your recommendations, the overall word count of the manuscript has regretfully increased. We hope you will find that the density and clarity of the discussion are nonetheless vastly improved.

2. Distinction between direct findings and literature-based inference

“ While the core hypothesis is intriguing, current inferences extend beyond what the existing data support; the narrative would be more coherent if there were a clearer distinction between direct findings (e.g., "GCLC inhibition in monocytes") and mechanistic inferences drawn from external literature (e.g., "this should trigger endothelial apoptosis and DIC") ”

We agree that the original text did not consistently signal which statements were supported by our own data and which extended that data using external literature. We have revised Section 3.2 to make this distinction explicit at each point of inference. For example:

While our whole-blood transcriptomic data cannot directly confirm endothelial cell fate, independent literature indicates that suppression of mitophagy initiation and execution leads to the accumulation of damaged mitochondria. Consequently, we infer that this sequence would trigger cytochrome c release...[lines 440-444]

And, where a claim is a direct finding rather than an inference:

“Our deconvolution analysis demonstrates that GCLC and SLC25A39 suppression co-localizes with NLRP3 transcript upregulation in the same myeloid populations. Based on this convergence, we propose that the relationship... may represent a highly coordinated pathophysiological axis.” [lines 562-567]

We have applied this pattern : explicit self-attribution for direct findings, and explicit "independent literature indicates" framing for inference throughout the revised Section 3.2. We also softened residual unhedged language elsewhere in the same section (e.g., "it is this severe bioenergetic failure that physically forces cardiolipin to flip" is now "thought to promote"; "Nrf2 suppression further amplified this entire process" is now "is proposed to amplify this process further").

3. Redundancyand schematic diagram 

“It is recommended to streamline the discussion, eliminate redundancies, and include a schematic diagram to aid reader comprehension of this multi-step model.”  

We identified and removed two redundant passages: a near-verbatim duplicate sentence describing the clinical failure of N-acetylcysteine, and a restatement of the core GCLC/SLC25A39/NLRP3 finding that had accumulated a fifth near-identical occurrence in the Discussion (which also carried an incorrect citation attributing our own transcriptomic result to external references). [troughout the manuscript] We have included three schematic figures that have been improved and enhanced to aid reader comprehension of this multi-step model: Figure 3 illustrates the proposed mechanistic cascade from Nrf2 suppression through GCLC/SLC25A39 failure to NLRP3 inflammasome activation, and Figure 4 illustrates the proposed dual-intervention therapeutic strategy. [troughout the manuscript]

4. Study limitationsanddefinitive therapeutic claims

“Most importantly, study limitations should be articulated more clearly, and definitive therapeutic claims—such as those regarding the efficacy of intravenous glutathione combined with honokiol—should be avoided in the absence of experimental validation”

We agree with the reviewer for both arguments, section 3.8 now contains explicit limitations subsections, addressing, among other points, the observational and cross-sectional design of the correlational findings, the non-detection of PRKN, the functionally underpowered status of GSE28750 (n=10), the inability of transcript-level data to establish protein abundance or enzymatic activity, and the stratification to DIC. [lines 901-932]. We agree that the original text overstated the therapeutic proposal's current standing. Section 3.6 previously closed by stating that the mechanism behind prior antioxidant-trial failures was "now mechanistically legible" and that our proposed intervention was "the first to address all three levels of the failure simultaneously." We have removed both statements; the section now ends with the CITRIS-ALI trial result itself, without extending it into a claim about our own intervention's mechanistic certainty. We have also added an explicit statement that the combined GSH/hinokitiol strategy lacks direct experimental validation and remains a theoretical hypothesis requiring rigorous preclinical evaluation. [lines 787-820]

Summary

We thank the Reviewer for an assessment that identified a consequential gap between what our data shows and how confidently we had described it. We have condensed the Discussion's most review-like section by approximately 35%, made the findings/inference distinction explicit and consistent, removed identified redundancies, confirmed two schematic figures are in place, expanded the limitations section, and removed the remaining unhedged therapeutic claims. We believe these changes bring the manuscript's tone perfectly in line with what the underlying bioinformatic analysis can actively support.

 

Author Response File: Author Response.pdf

Reviewer 3 Report

Comments and Suggestions for Authors This manuscript reports an interesting bioinformatic study on the transcriptional regulation of myeloid-driven inflammatory pathways, using multi-dataset deconvolution and pathway enrichment pipelines to identify putative metabolic vulnerabilities. While the integration of bulk transcriptomic platforms offers a consistent exploratory architecture, the work would benefit greatly from clarification of platform normalization steps, moderation of unverified statements about myeloid convergence, and alignment of the mechanistic narrative toward the strongly expressed receptor-mediated mitophagy pathways, rather than classical Parkin components that are not detectable.  Major Comments 1. The manuscript is heavily dependent on xCell deconvolution, which is used to seperate bulk transcriptomic signals from whole blood into cell-type-specific components. However, the paper admits that GSE28750 is functionally underpowered (n=10) and is merely directional confirmation. Authors should clarify how they normalized potential platform batch effects between Illumina (GSE54514) and Affymetrix (GSE13904) arrays before pooling or cross-validating correlation metrics as technical platform differences can heavily skew deconvolution enrichment scores. 2. The main hypothesis is based on the co-localization of GCLC suppression, SLC25A39 downregulation and NLRP3 upregulation in the myeloid compartment . Since this is established solely by bioinformatic correlates (rho values) from cross-sectional data sets, the text must explicitly down-tone definitive causal language unless supported by preliminary wet-lab data. The authors correctly note in Section 3.8.2 that experimental testing (such as the proposed in vitro HUVEC/HMEC-1 models) is required to prove that myeloid GCLC/SLC25A39 suppression is upstream of NLRP3 activation, rather than a parallel epiphenomenon.  3. The classical Parkin gene (PRKN or PARK2) was not detectable in all three microarray platforms and the authors skipped the classic PINK1/Parkin arm and focused on BNIP3L and FUNDC1 receptor-mediated mitophagy.  4. Given the emphasis on the role of Parkin in the introductory framework and text (Section 3.2.1), the authors should consider re-organizing this section to ensure the narrative focuses exclusively on the receptor-mediated pathways (BNIP3L/FUNDC1) that showed strong baseline expression in the datasets.Pharmacodynamic  5. The therapeutic strategy combines intravenous glutathione with hinokitiol, a Fe-S cluster ionophore, in an effort to protect SLC25A39 from AFG3L2-mediated proteolysis. The known toxicity profiles of iron ionophores, and the hard ceiling of reductive stress (over-reducing thioredoxin-2/peroxiredoxin-III systems) should have led to a more rigorous pharmacokinetic or safety roadmap of administering hinokitiol concomitantly with high-dose IV GSH in a critical care septic shock setting. Minor Comments 1. For instance, the descriptions of Table 3 and Table 4 contain formatting anomalies, such as the substitution of "A" for negative/positive signs in symbols for log fold changes around lines 612–622, as well as minor reference formatting overlaps. 2. Make sure all text nodes in Figure 1 and schematic Figure 3 are completely readable. 3. Check the formatting of gene and protein symbols throughout the manuscript. All  gene symbols (GCLC, GCLM, SLC25A39, NLRP3, GSDMD, AFG3L2) are need to be italicized in the main text.  

 

Author Response

Dear Respected Reviewer 3,

We sincerely thank you for your rigorous evaluation of our manuscript. Your assessment identified critical areas for clarification regarding our methodological approach to platform batch effects, narrative focus on mitophagy pathways, and vital therapeutic safety considerations. We have taken your recommendations seriously, and the response below reflects a substantive recalibration of the manuscript's narrative and structural focus. We greatly appreciate the time and effort directed toward providing this constructive feedback. Point-by-point responses are provided below, with manuscript revisions highlighted in red and accompanied by corresponding line numbers.

1. Platform normalization and xCell deconvolution

“The manuscript is heavily dependent on xCell deconvolution, which is used to seperate bulk transcriptomic signals from whole blood into cell-type-specific components. However, the paper admits that GSE28750 is functionally underpowered (n=10) and is merely directional confirmation. Authors should clarify how they normalized potential platform batch effects between Illumina (GSE54514) and Affymetrix (GSE13904) arrays before pooling or cross-validating correlation metrics as technical platform differences can heavily skew deconvolution enrichment scores.“

We thank the Reviewer for highlighting this crucial technical point. To entirely mitigate platform-specific bias between the Illumina (GSE54514) and Affymetrix (GSE13904, GSE28750) arrays, we deliberately did not pool raw expression values or xCell enrichment scores across datasets. Instead, all statistical analyses were restricted to strictly within-dataset comparisons. We utilized Spearman’s rank correlation, which is inherently invariant to monotonic differences in platform dynamic range, ensuring correlations were independent of underlying intensity scales. Furthermore, we omitted standard cross-platform batch correction algorithms (e.g., ComBat) because dataset identity is completely confounded with distinct patient cohorts, meaning global batch correction risks suppressing true biological variance. This conservative, rank-based analytical approach has been prominently emphasized in the revised Section 4.3.  [lines 1026-1038]

2. Definitive causal language based on bioinformatic correlates

“The main hypothesis is based on the co-localization of GCLC suppression, SLC25A39 downregulation and NLRP3 upregulation in the myeloid compartment. Since this is established solely by bioinformatic correlates (rho values) from cross-sectional data sets, the text must explicitly down-tone definitive causal language unless supported by preliminary wet-lab data. The authors correctly note in Section 3.8.2 that experimental testing (such as the proposed in vitro HUVEC/HMEC-1 models) is required to prove that myeloid GCLC/SLC25A39 suppression is upstream of NLRP3 activation, rather than a parallel epiphenomenon.”

We entirely agree with this assessment. We have extensively revised the manuscript (Abstract, Sections 3.2, and 3.6) to remove definitive causal claims, replacing them with terminology that accurately reflects theoretical inference based on our co-localization findings (e.g., "hypothesize," "we propose", “transcript upregulation”). We have ensured that the manuscript explicitly frames the progression from mGSH depletion to DIC as an inference supported by independent literature, not a direct proof of our cross-sectional datasets. [troughout the manuscript]

3 & 4. Focus on receptor-mediated mitophagy (BNIP3L/FUNDC1)

“The classical Parkin gene (PRKN or PARK2) was not detectable in all three microarray platforms and the authors skipped the classic PINK1/Parkin arm and focused on BNIP3L and FUNDC1 receptor-mediated mitophagy. Given the emphasis on the role of Parkin in the introductory framework and text (Section 3.2.1), the authors should consider re-organizing this section to ensure the narrative focuses exclusively on the receptor-mediated pathways (BNIP3L/FUNDC1) that showed strong baseline expression in the datasets.”

We thank you for this excellent structural recommendation. We acknowledge that classical Parkin (PRKN) mRNA was below the detectable probe threshold across all three microarray platforms. Consequently, we have reorganized Section 3.2.1 and the broader mitophagy discussion to focus exclusively on receptor-mediated pathways. We have highlighted that BNIP3L and FUNDC1 show highly robust and consistent baseline expression across both the large cross-sectional cohort (GSE54514) and the isolated monocyte cohort (GSE46955). The text now explicitly posits that mitochondrial glutathione collapse likely disrupts this receptor-mediated clearance within myeloid cells. Phosphatidylserine externalisation, tissue-factor–bearing microparticle shedding, thrombomodulin loss, and PAI-1–driven fibrinolytic suppression follow as previously described in this section and are not receptor-specific. Only the upstream trigger has been revised [lines 405-449]

5. Pharmacodynamic and Safety Considerations for Hinokitiol and IV GSH

“The therapeutic strategy combines intravenous glutathione with hinokitiol, a Fe-S cluster ionophore, in an effort to protect SLC25A39 from AFG3L2-mediated proteolysis. The known toxicity profiles of iron ionophores, and the hard ceiling of reductive stress (over-reducing thioredoxin-2/peroxiredoxin-III systems) should have led to a more rigorous pharmacokinetic or safety roadmap of administering hinokitiol concomitantly with high-dose IV GSH in a critical care septic shock setting.”

We thank the reviewer for this vital clinical consideration that we previously under-addressed. We have updated Section 3.6 to explicitly outline the strict safety constraints of this proposed intervention. We added language detailing the ceiling imposed by reductive stress, noting that supraphysiological GSH concentrations can impair mitochondrial electron transport chain function by over-reducing the thioredoxin-2 and peroxiredoxin-III systems. Furthermore, we have added explicit statements acknowledging the known toxicity profiles of iron ionophores, stipulating that a rigorous pharmacokinetic and safety roadmap for hinokitiol is an absolute prerequisite before progressing to clinical dose-finding studies. [lines 787-820]

Minor Comments

1. Table 3/Table 4 formatting (substitution of “A” for +/− signs, ~lines 612–622): we were unable to locate this artifact from the manuscript text, as it appears to be a font/symbol-encoding issue (a character typed in a symbol font rendering as a different glyph than intended) that is only visible in the rendered document, not in the underlying text. We have flagged this for correction and would appreciate the Reviewer's specific cell reference, or can review directly if a fresh export of the affected tables is provided.
2. Figure 1 and Figure 3 text readability: we have reviewed both figures and increased font sizes and contrast where labels were cramped or low-resolution; both have been re-exported at higher resolution.
3. Gene/protein symbol italicization: all gene symbols (GCLC, GCLM, NFE2L2, NLRP3, GSDMD, PINK1, PRKN, BNIP3L, FUNDC1, SLC25A39, SLC25A40, AFG3L2) have been italicized throughout the main text, per standard nomenclature convention, while protein products and dataset/study names are left in regular type.

 

Summary

We thank the Reviewer for identifying the issues precisely, particularly the hinokitiol safety roadmap, which had not identified raised before. We believe these targeted revisions directly address the methodological and narrative concerns raised. By clarifying our batch-effect avoidance strategy, centering the mitophagy discussion on detectable transcripts (BNIP3L/FUNDC1), and outlining a rigorous safety framework for the proposed therapy, the manuscript is now substantially more precise and clinically grounded. We thank the Reviewer again for an evaluation that has greatly enhanced the rigor of this study.

 

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

I am very disappointed that the authors were so careless in addressing the issues mentioned. Several of central concerns are still not actually resolved in the manuscript, despite the response letter saying they are. The principal concern regarding overinterpretation of computational data remains only partially resolved and internal inconsistencies are still present. 
1. Response letter states that the GSE54514 xCell analysis was restricted to Day-1 samples and analyzed by Spearman correlation, whereas the revised manuscript refers to an LMM-based xCell analysis and does not describe a Day-1 restriction. The exact analysis generating the reported cell-type coefficients must therefore be clarified and made reproducible.
In addition, xCell-derived associations are still repeatedly described as “cell-intrinsic suppression”. NLRP3/GSDMD transcript abundance is still interpreted as inflammasome activation, NFE2L2 mRNA as NRF2 activation, and recovery-phase AFG3L2–SLC25A39 co-transcription as evidence that newly synthesized SLC25A39 undergoes proteolytic cleavage. These conclusions exceed what the present transcriptomic datasets demonstrate.
2. The manuscript itself acknowledges that hinokitiol lacks human clinical data and has unresolved safety concerns, yet the Abstract recommends combining it with intravenous GSH and the Conclusion states that such combination “must” be used. This should be reframed strictly as a preclinical hypothesis.
3. Several internal inconsistencies require correction, including 295 versus 203 sepsis patients, the SIRS/sepsis composition of GSE13904, the reported GSE46955 sample numbers, and the description of the statistical method used in the Abstract (“Mann-Whitney U with Benjamini-Hochberg correction”, though in GSE54514 was reanalyzed with a linear mixed-effects model)
4. NLRP3 and GSDMD transcript expression is not equivalent to inflammasome/pyroptotic activation. The response letter says the authors agree. Yet the Abstract still says the transcript patterns suggest “synthesis failure, import failure, and inflammasome activation” and the Conclusion says the affected myeloid populations are “driving NLRP3 inflammasome activation”. 
5. The response letter correctly acknowledges that GSE13904 is a pediatric, not the previously claimed adult cohort. The revised Limitations also correctly describe it as a pediatric cohort. Yet in Methods the authors call all 158 subjects “mixed-severity sepsis pediatric patients” and then calculate a total of 203 sepsis patients across the three cohorts. This is wrong.
6. The Abstract states that combining intravenous GSH with hinokitiol “is recommended”, and the Conclusion says intravenous GSH “must be combined with hinokitiol.”. That is incompatible with the safety discussion and with hypothesis-generating nature of the study.
7. For a manuscript whose central contribution is a reanalysis of public transcriptomic datasets, “code available on request” is not enough. The revised manuscript reports substantial custom processing, LMM analysis, xCell analysis, z-score transformations, multiple-correction procedures, and cohort-specific handling. I strongly recommend depositing the full analysis code and sample selection tables in a public repository or Supplementary Materials. 

Author Response

Respected Reviewer 1,

We sincerely thank you for your critical and meticulous evaluation of our revised manuscript. We recognize that our previous response did not adequately execute the requested modifications, leaving several internal inconsistencies and overinterpretations in the text. We have now thoroughly overhauled the manuscript to ensure absolute mathematical precision, objective description of transcriptomic data, and full methodological transparency. 

Comment 1:

Response letter states that the GSE54514 xCell analysis was restricted to Day-1 samples and analyzed by Spearman correlation, whereas the revised manuscript refers to an LMM-based xCell analysis and does not describe a Day-1 restriction. The exact analysis generating the reported cell-type coefficients must therefore be clarified and made reproducible. In addition, xCell-derived associations are still repeatedly described as “cell-intrinsic suppression”. NLRP3/GSDMD transcript abundance is still interpreted as inflammasome activation, NFE2L2 mRNA as NRF2 activation, and recovery-phase AFG3L2–SLC25A39 co-transcription as evidence that newly synthesized SLC25A39 undergoes proteolytic cleavage. These conclusions exceed what the present transcriptomic datasets demonstrate.

We have removed the linear mixed-effects model from the analysis entirely, which resolves the inconsistency directly and prevents any inconsistencies. All longitudinal cohorts (GSE54514 and GSE13904) are now uniformly restricted to Day-1 baseline samples per patient to prevent pseudoreplication, and analyzed with the Mann-Whitney U test (Benjamini-Hochberg corrected) for differential expression and Spearman's rank correlation for xCell-derived cell-type associations. This approach is now stated identically in the Abstract, Methods Section 4.3, and the Table 2/3 captions. On overinterpretation, each item has been reframed to stay at the transcript/correlational level:

1. Section 2.2.3 no longer calls the xCell associations “cell-intrinsic suppression”, it now states explicitly that the cross-platform correlations indicate reduced bulk transcript abundance tracking with myeloid population expansion.[troughout the manuscript]
2. NLRP3/GSDMD transcript abundance is now described as “inflammasometranscriptonal upregulation” throughout the Abstract, Introduction, Results Section 2.3, and Conclusion, with causal direction explicitly flagged as requiring experimental testing. [lines 108;137;292]
3. NFE2L2 mRNA is now framed as transcript-level uncoupling.[lines 615-620]
4. The AFG3L2–SLC25A39 co-transcription finding is now explicitly hedged as a hypothesis (“we hypothesize that this expression profile may reflect a compensatory state wherein newly synthesized transporters remain vulnerable to proteolytic cleavage”) rather than asserted as evidence of cleavage.[lines 1069-1071]

Comment 2:

The manuscript itself acknowledges that hinokitiol lacks human clinical data and has unresolved safety concerns, yet the Abstract recommends combining it with intravenous GSH and the Conclusion states that such combination “must” be used. This should be reframed strictly as a preclinical hypothesis.

The Abstract and Conclusion have been reworded so that the combination is presented strictly as a preclinical hypothesis rather than a recommendation. The Abstract now states that bypassing the enzymatic bottleneck “could mechanistically address these findings” but that “this remains strictly a preclinical hypothesis that requires extensive investigation to resolve existing safety concerns, particularly the potential for ionophore toxicity in humans.” The Conclusion carries the same hedged framing and no longer contains the word “must.”[lines 49-53;1078-1082]

Comment 3:

Several internal inconsistencies require correction, including 295 versus 203 sepsis patients, the SIRS/sepsis composition of GSE13904, the reported GSE46955 sample numbers, and the description of the statistical method used in the Abstract (“Mann-Whitney U with Benjamini-Hochberg correction”, though in GSE54514 was reanalyzed with a linear mixed-effects model)

All patient counts have been corrected and cross-checked for consistency across the Abstract, Methods, and Table 5. The manuscript now uniformly reports n=200 across the three whole-blood cohorts (144 sepsis, 56 controls): GSE54514 (35 sepsis + 18 controls = 53), GSE13904 (99 sepsis + 18 controls = 117), and GSE28750 (10 sepsis + 20 controls = 30). The earlier 295/203 figures have been removed. GSE13904's composition is now stated explicitly as excluding SIRS-only samples (Table 5; Limitations Section 3.8.9; line 989). GSE46955 sample numbers are stated consistently as n=14 individuals / 22 profiles wherever cited. The Abstract's statistical-method description has been corrected to match Methods 4.3 exactly:

 “All cohorts were strictly filtered to Day-1 baseline samples to prevent pseudoreplication. Differential expression was evaluated via Mann-Whitney U with Benjamini-Hochberg correction, with xCell deconvolution resolving bulk signals into cell-type-specific components via Spearman correlation.” [lines 22-25]

The linear mixed-effects model has been removed from the analysis (see response to Comment 1).

Comment 4:

NLRP3 and GSDMD transcript expression is not equivalent to inflammasome/pyroptotic activation. The response letter says the authors agree. Yet the Abstract still says the transcript patterns suggest “synthesis failure, import failure, and inflammasome activation” and the Conclusion says the affected myeloid populations are “driving NLRP3 inflammasome activation”.

We agree, and we apologize that the earlier revision did not carry this correction through consistently. The Abstract [lines 35-38], Introduction [lines 105-110], Results Section, 2.2.1 [lines 132-135] , 2.2.3 [lines 173-179]  , 2.4 [lines 285-287] and Conclusion [lines 1056-1063] have all been revised. The Conclusion no longer states that the affected myeloid populations are “driving NLRP3 inflammasome activation”.

Comment 5:

The response letter correctly acknowledges that GSE13904 is a pediatric, not the previously claimed adult cohort. The revised Limitations also correctly describe it as a pediatric cohort. Yet in Methods the authors call all 158 subjects “mixed-severity sepsis pediatric patients” and then calculate a total of 203 sepsis patients across the three cohorts. This is wrong.

Corrected. GSE13904 is now described consistently as a pediatric cohort throughout Methods Section 4.1 [lines 976-983], Table 5, and the Limitations (Section 3.8.9), which now states explicitly that SIRS-only samples were excluded and that the 99 sepsis-cohort subjects are sepsis/septic-shock patients, describing their actual states of sepsis instead of referring to them as “mixed-severity”.

 The patient totals have been corrected accordingly: 99 + 18 controls = 117 for GSE13904, and 144 sepsis + 56 controls = 200 across all three cohorts, replacing the erroneous 158/203 figures.

Comment 6:

The Abstract states that combining intravenous GSH with hinokitiol “is recommended”, and the Conclusion says intravenous GSH “must be combined with hinokitiol.”. That is incompatible with the safety discussion and with hypothesis-generating nature of the study.

As described in our response to Comment 2, the Abstract and Conclusion have been reworded to remove “is recommended” and “must be combined.” Both now explicitly frame the combination as a preclinical, mechanistically-motivated hypothesis pending safety and efficacy validation, consistent with the hinokitiol safety discussion elsewhere in the manuscript.

Comment 7:

For a manuscript whose central contribution is a reanalysis of public transcriptomic datasets, “code available on request” is not enough. The revised manuscript reports substantial custom processing, LMM analysis, xCell analysis, z-score transformations, multiple-correction procedures, and cohort-specific handling. I strongly recommend depositing the full analysis code and sample selection tables in a public repository or Supplementary Materials.

We agree, and have deposited the complete analysis pipeline in a public GitHub repository (https://github.com/felixbadiu9/The-enzymatic-mitochondrial-import-bottleneck-in-Sepsis), including the R scripts for data extraction, Day-1 deduplication, differential expression, xCell deconvolution, and cell-population shift analysis, together with the sample-selection matrices needed to reproduce the cohort composition reported in Table 5. This repository is also archived in the Supplementary Materials. The Methods (Section 4.3) and Data Availability statement have both been updated accordingly and no longer say “available on request.” [lines 1037-1042 ; Data Availability]

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

I would like to commend the authors for their diligent and thorough revision of the manuscript. The additional data provided, particularly the in vivo transgenic mouse model and the pharmacological rescue experiments using Mdivi-1, successfully address the previous concerns regarding causality and the mechanistic role of mitochondrial fission. The manuscript is now much more persuasive, and the logic connecting Tau-induced mitochondrial dysfunction to cardiac pathology is clearly articulated. I also appreciate the improved clarity in the statistical methods and the more detailed discussion regarding the limitations of the Mdivi-1 inhibitor. The manuscript is now well-structured, the experiments are logically presented, and the conclusions are well-supported by the evidence provided. I have no further concerns and believe the work is ready for publication.

Comments on the Quality of English Language

none

Author Response

Comment : 

I would like to commend the authors for their diligent and thorough revision of the manuscript. The additional data provided, particularly the in vivo transgenic mouse model and the pharmacological rescue experiments using Mdivi-1, successfully address the previous concerns regarding causality and the mechanistic role of mitochondrial fission. The manuscript is now much more persuasive, and the logic connecting Tau-induced mitochondrial dysfunction to cardiac pathology is clearly articulated. I also appreciate the improved clarity in the statistical methods and the more detailed discussion regarding the limitations of the Mdivi-1 inhibitor. The manuscript is now well-structured, the experiments are logically presented, and the conclusions are well-supported by the evidence provided. I have no further concerns and believe the work is ready for publication.

We sincerely thank the reviewer for their time and effort in evaluating our manuscript. We are pleased to hear that there are no further concerns and that you consider the work ready for publication. We greatly appreciate your positive recommendation and your support of this manuscript.

 

Reviewer 3 Report

Comments and Suggestions for Authors

The authors have addressed all the concerns raised in the review process in a very detailed and the modifications greatly improved the clarity and quality of the manuscript. I am satisfied with the changes made, and recommend the manuscript for final acceptance in its current form.

Author Response

Comment

"The authors have addressed all the concerns raised in the review process in a very detailed and the modifications greatly improved the clarity and quality of the manuscript. I am satisfied with the changes made, and recommend the manuscript for final acceptance in its current form."

We sincerely thank the reviewer for their time, their positive feedback, and their recommendation for acceptance.

Round 3

Reviewer 1 Report

Comments and Suggestions for Authors

I appreciate the extensive revision. Overall, the revised manuscript is substantially stronger and the remaining concerns are now relatively focused. However, few important issues remain:

1. xCell-derived correlations are still occasionally interpreted as evidence of within-cell transcriptional regulation. Statements that deconvolution reveals “true per-cell NLRP3 upregulation,” that GCLM bulk upregulation is “entirely driven” by myeloid expansion, or that GSDMD elevation occurs primarily within specific myeloid compartments exceed what xCell enrichment correlations can establish. These sentences should be rewritten consistently as associations between bulk gene expression and estimated cell-type enrichment.
2. The aggregate AFG3L2 - SLC25A39 analysis in GSE46955 requires statistical reconsideration. The dataset contains 22 samples from 14 individuals, including paired acute and recovery samples from the same eight septic patients. A conventional Spearman correlation across all 22 samples does not account for the non-independence of repeated observations. The correlation should therefore be reanalyzed using an approach appropriate for repeated measures, or presented descriptively if the available sample size does not permit a reliable longitudinal model.
3. Additional revisions should include replacing “mitophagic failure” with transcript-level terminology unless functional mitophagy is directly measured, and harmonizing the cautious therapeutic wording of the Abstract with the still categorical statements in the Introduction that NAC “proves futile” and intravenous GSH is an “essential prerequisite.”

Once these issues are addressed, the work could be considered for publication.

Author Response

Respected Reviewer 1,

 

We wish to extend our sincere appreciation for your rigorous reading of the manuscript and highly constructive feedback. Your precise insights regarding the statistical handling of the longitudinal cohort and the inferential limits of computational deconvolution have significantly strengthened the methodological rigor and scientific clarity of this paper.

 

Comment 1:

xCell-derived correlations are still occasionally interpreted as evidence of within-cell transcriptional regulation. Statements that deconvolution reveals “true per-cell NLRP3 upregulation,” that GCLM bulk upregulation is “entirely driven” by myeloid expansion, or that GSDMD elevation occurs primarily within specific myeloid compartments exceed what xCell enrichment correlations can establish. These sentences should be rewritten consistently as associations between bulk gene expression and estimated cell-type enrichment.

We agree with the reviewer that xCell computational deconvolution estimates cell-type enrichment from bulk signatures and cannot establish direct per-cell transcriptional regulation.

We have meticulously revised the manuscript (specifically in Sections 2.2.1 [lines 137-139] , 2.2.2 [lines 141-143] , 2.2.4 [lines 187-189] and 3.4.2 [lines 679-680;682-683]  ) to eliminate claims of "true per-cell" expression, "entirely driven," and direct cellular origination. All relevant findings are now explicitly and consistently framed as statistical associations between bulk transcript abundance and estimated cell-type enrichment scores.

Comment 2:

The aggregate AFG3L2 - SLC25A39 analysis in GSE46955 requires statistical reconsideration. The dataset contains 22 samples from 14 individuals, including paired acute and recovery samples from the same eight septic patients. A conventional Spearman correlation across all 22 samples does not account for the non-independence of repeated observations. The correlation should therefore be reanalyzed using an approach appropriate for repeated measures, or presented descriptively if the available sample size does not permit a reliable longitudinal model.

We thank the reviewer for identifying the statistical limitation of utilizing a standard Spearman correlation across longitudinal samples containing repeated measures. To account for the non-independence of the 22 samples derived from the 8 patients (measured during acute and recovery phases) alongside the healthy controls, we have re-analyzed the GSE46955 dataset using a linear mixed-effects model (LMM). By fitting SLC25A39 transcript abundance as a function of AFG3L2 with a random intercept per patient, the model confirmed a significant positive within-patient relationship (beta = 0.404, p = 0.0122), verifying that this coregulation remains significant independently of patient-specific baseline variance. The Abstract, Section 2.4, Section [lines 247-262]  4.3 (Methods) [lines 1046-1056], and Section 5 (Conclusions) [lines 1087-1090] have been fully updated to report this robust LMM methodology and its results in place of the prior Spearman correlation.

Comment 3:

Additional revisions should include replacing “mitophagic failure” with transcript-level terminology unless functional mitophagy is directly measured, and harmonizing the cautious therapeutic wording of the Abstract with the still categorical statements in the Introduction that NAC “proves futile” and intravenous GSH is an “essential prerequisite.”

The manuscript has been revised to strictly differentiate between the transcriptional suppression measured within our bioinformatic cohorts and the functional mitophagic failure established in independent experimental literature. Section 3.2.1 now features an explicit introductory clarification to ensure our bioinformatic data is not over-extrapolated, reading:

 "The mechanistic discussion below extrapolates from the transcriptional suppression observed in our cohorts to the functional mitophagic failure established by independent experimental models." [lines 395-397]

The title of section 3.2.1 remains unchanged, as the section itself discusses well studied mechanisms rather than the results themselves, which are mentioned only once, to create a directional convergence. Furthermore, we have attenuated the manuscript's therapeutic terminology. The previously categorical statements in the Introduction asserting that NAC "proves futile" and intravenous GSH is an "essential prerequisite" have been appropriately softened to state that NAC "may prove insufficient" and GSH "may represent a necessary prerequisite," aligning seamlessly with the cautious, preclinical hypothesis framing established in the Abstract.

 

Author Response File: Author Response.pdf