Scientific Manuscript Reviewer

Peer Review Report

Manuscript: Effects of 16:8 Time-Restricted Eating on Gut Microbiome Diversity and Glycemic Control in Adults with Type 2 Diabetes: A 12-Week Randomized Controlled Trial Type: Original Research Recommendation: Major Revision

1. Summary

The authors randomized 42 metformin-treated adults with T2D to 12 weeks of 16:8 time-restricted eating (10:00–18:00) or standard ADA dietary advice. They report increased Shannon diversity and Akkermansia abundance, greater HbA1c reduction (−0.6 vs −0.2%), and greater weight loss (−2.8 vs −0.9 kg) with TRE. The question is clinically relevant and the randomized design is a real asset in a field dominated by cross-sectional microbiome data. However, the central mechanistic claim, that microbiome remodeling mediates the metabolic benefit, is not tested by any analysis in the manuscript. Several reported p-values appear inconsistent with the summary statistics. Key trial-reporting elements are also missing: registration, a pre-specified primary outcome, a power calculation, and an ITT analysis. In its current form the work reads best as a pilot/feasibility RCT, and it should be reframed as one.

2. Major Issues

M1. The mediation claim is unsupported by any analysis (Severity: Critical, blocking)

The Abstract ("microbiome remodeling may partly mediate the metabolic benefits") and Conclusion ("suggesting microbiome remodeling as a candidate mechanism") imply a causal pathway. The analysis only shows two parallel group-level changes. No correlation, regression, or formal mediation analysis links individual microbiome change to individual glycemic change. The Discussion concedes that microbiome changes may simply follow caloric restriction and weight loss. That concession contradicts the Abstract and Conclusion.

Suggested fixes:

• Remove mediation language from the Abstract, Discussion, and Conclusion, or support it with data.
• At minimum, report the participant-level associations between ΔShannon and ΔHbA1c, and between ΔAkkermansia and ΔHbA1c, with and without adjustment for Δweight.
• A formal mediation analysis would be severely underpowered at n≈39. If attempted, label it explicitly as exploratory and report CIs rather than p-values.

M2. Weight loss and unmeasured energy intake confound all outcomes (Critical)

The TRE arm lost about 1.9 kg more than controls. Weight loss by itself is known to improve HbA1c and can shift microbiome composition. Dietary intake was not measured (no 24-h recalls, food records, or doubly labeled water). The design therefore cannot attribute any effect to meal timing as opposed to eating less. This limits the interpretation of the entire paper, not only the mechanistic claim.

Suggested fixes:

• Adjust HbA1c and microbiome outcomes for weight change (ANCOVA) and report whether between-group effects persist. Frame this as sensitivity analysis, not proof.
• Report any available dietary data, including macronutrient and fiber content if the smartphone logs captured food content. Fiber intake is a major determinant of Shannon diversity and Akkermansia, so its absence is a particular problem for the microbiome outcomes.
• State plainly in the Abstract that energy intake was not quantified.

M3. Reported p-values appear inconsistent with the summary statistics (Critical, must be resolved)

I recomputed the between-group tests from the reported means ± SD. I assumed about 19 TRE and 20 control participants analyzed, and Welch/Student two-sample t-tests on change scores:

If the ± values are SDs, the reported p-values are far too conservative. If they are SEs, the implied SDs (about 1.3–1.9% for HbA1c) would make the HbA1c difference non-significant. Neither reading matches the reported values. I may be missing an analytic detail, such as a different test, different n, or an adjusted model. Either way, the authors must reconcile this.

Suggested fixes:

• State explicitly whether ± denotes SD or SE, give the n analyzed per arm for each outcome, and name the exact test used.
• Report between-group differences with 95% CIs, not only p-values.
• Consider having the analysis independently re-run.

M4. Within-group versus between-group inference, particularly for Akkermansia (Major)

• The Akkermansia result (2.1-fold, p=0.03) is a within-group test, and the control arm is described as "unchanged." A significant change in one arm and a non-significant change in the other does not show that the arms differ (the "difference in significance" fallacy). A between-group test of Akkermansia change is required.
• The Abstract headlines the within-group Shannon comparison (3.21 → 3.58, p=0.01). In an RCT, the between-group comparison (p=0.03) is the valid causal contrast and should be primary.
• Section 2.5 describes only between-group tests. The method used for the within-group p-values (paired t? Wilcoxon signed-rank?) is not stated.
• Shannon values are reported as mean ± SD, yet a rank-based test was used. Report medians/IQR to match, or justify.

Suggested fix: Use ANCOVA (week-12 value adjusted for baseline, site, and possibly sex) or a linear mixed model as the primary analysis for all continuous outcomes. Relegate within-group tests to descriptive supplementary material.

M5. Multiple comparisons, compositional methods, and taxonomic resolution (Major)

• Multiplicity: Fourteen genera were tested without correction. At a Bonferroni threshold (0.05/14 ≈ 0.0036), the Akkermansia p=0.03 would not survive, and it would very likely not survive Benjamini–Hochberg FDR either. The authors acknowledge this in the Discussion but still present the finding as a headline result.
• Selection of the 14 genera: Were these pre-specified, and if so, where? Or were they chosen after inspecting the data? This must be stated. If post hoc, the Akkermansia result is hypothesis-generating only.
• Compositionality: Relative abundance data from 16S sequencing are compositional, and a fold-change in relative abundance does not equal a change in absolute load. Use compositionally aware methods such as ANCOM-BC2, ALDEx2, or MaAsLin2 with appropriate transformation, and report FDR-adjusted q-values. qPCR for Akkermansia would provide absolute quantification and would be a valuable addition.
• Species-level claim: V3–V4 16S amplicons generally cannot reliably resolve species. The manuscript names Akkermansia muciniphila throughout. Unless ASVs were verified by species-specific qPCR or shotgun metagenomics, refer to the genus Akkermansia (or "an Akkermansia ASV").

M6. Per-protocol analysis only; ITT absent (Major)

ITT is the standard primary analysis for an RCT. With only 3 dropouts, ITT is straightforward: use a linear mixed model with all randomized participants, or multiple imputation. Per-protocol can then be a sensitivity analysis. Please also report the reasons for loss to follow-up by arm.

M7. Trial registration, primary outcome, and sample size justification (Major)

• Registration: No registration number (e.g., ClinicalTrials.gov) is given. Prospective registration is a requirement for RCT publication in most major journals, including those following ICMJE policy. If the trial was registered, provide the ID and confirm that reported outcomes match the registered primary and secondary outcomes.
• Primary outcome: The hypothesis names both microbiome diversity and glycemic control, but no single primary endpoint is designated. Please specify it and treat all others as secondary.
• Power: No sample size calculation is reported. If none was done a priori, say so and reframe the study as a pilot/feasibility trial. The effect estimates would then serve to inform the power calculation for a confirmatory trial.
• Reporting standard: Please provide a CONSORT flow diagram and checklist. A CONSORT extension for pilot trials may be appropriate.

M8. Allocation concealment conflated with blinding (Major, methodological reporting)

Section 2.1 states that "allocation was not concealed from participants or dietitians due to the nature of the intervention." This conflates two separate safeguards:

• Allocation concealment hides the upcoming assignment from recruiters before enrollment. It is always feasible, for example with sealed opaque envelopes or central randomization. If it was not done, this is a meaningful risk of selection bias.
• Blinding of participants after assignment is indeed infeasible for TRE. Outcome assessors, laboratory staff, and the bioinformatics and statistical analysts can still be blinded.

Suggested fix: Clarify what was actually done for each safeguard. State whether the microbiome and statistical analyses were performed blinded to arm. Report whether randomization was stratified or blocked by site, which matters with two clinics.

M9. Control condition and adherence measurement (Major)

• Attention imbalance: The SDA arm received ADA dietary counseling. It is unclear whether the TRE arm received equivalent contact time or any dietary counseling. Differences in contact and in dietary content (e.g., fiber advice in SDA) could influence both arms in ways unrelated to meal timing.
• Baseline and control eating windows: Neither arm's baseline eating window is reported. The control arm's eating window during the trial is also not reported. If controls already ate within about 10–11 hours, the timing contrast is smaller than implied. Please report eating-window duration by arm at baseline and during follow-up.
• Adherence: The 82% figure is self-reported, and the definition of an "adherent day" is not given. An objective proxy would substantially strengthen the paper, for example CGM-inferred meal timing or photo-timestamped logging. A dose–response analysis of adherence against outcomes would also help.

M10. Metformin as a microbiome confounder (Moderate)

Metformin itself alters gut microbiome composition, and several studies report increases in Akkermansia (e.g., work by Wu et al., 2017, Nat Med). The stable-dose requirement is appropriate. Still, the authors should report:

• metformin dose by arm;
• whether dosing timing shifted to fit the eating window, which could change GI exposure;
• any GI side effects and any medication changes during the trial.

3. Minor Issues

1. Unreported outcomes: Fasting glucose was measured (Section 2.4) but not reported in the Results. Report it, along with any other collected measures such as insulin, HOMA-IR, lipids, or CGM data.
2. Beta diversity: Beta diversity is not reported. Add PERMANOVA on Bray–Curtis and/or Aitchison distance, with between-group comparison of within-subject change.
3. Sequencing QC:
   • Report read depth per sample and rarefaction depth, if used.
   • Report negative extraction and PCR controls and positive controls (mock community).
   • State whether all samples were processed in a single batch, and whether baseline and week-12 samples from the same participant shared a run.
4. Stool covariates: Stool consistency (e.g., Bristol Stool Scale) and transit time are known to influence alpha diversity. Record or report them if possible, along with time of collection relative to the eating window.
5. HbA1c assays: HbA1c was measured at each clinic's local laboratory. Specify the assay methods and whether they are NGSP-certified. Adjust for site, since inter-laboratory variability matters when effects are about 0.4 percentage points.
6. Units: State HbA1c changes as percentage points and add mmol/mol, consistent with the journal's reporting conventions.
7. Hypoglycemia: Hypoglycemia risk is low with metformin monotherapy, but explicitly report hypoglycemia monitoring and events.
8. Physical activity: Report physical activity if it was captured, as it is a possible differential co-intervention.
9. Seasonality: Enrollment ran March–September, so follow-up spans seasons. Randomization mitigates this, but a brief comment on seasonal dietary variation would be helpful.
10. Introduction and literature:
    • The claim that TRE's microbiome effects in T2D "have not been directly tested in a randomized design" should be verified against a current search. RCTs of TRE in T2D exist, for example Che et al., 2021 (Nutr Diabetes) and Pavlou et al., 2023 (JAMA Netw Open). Some TRE microbiome work also exists in other populations (e.g., Xie et al., 2022, Nat Commun). I am not certain whether any prior RCT assessed the microbiome specifically in T2D, so please confirm and cite accurately.
    • Sutton et al. (2018) studied men with prediabetes under isocaloric, supervised feeding. It is more accurately described as such than as a "non-diabetic" trial. Its isocaloric design is also directly relevant to the authors' weight-confounding problem and is worth discussing.
    • The "530 million" prevalence figure corresponds to the IDF 2021 Atlas. Please check whether a more recent estimate should be cited.
11. Missing materials: Table 1 and Figure 2A are referenced but not provided in the excerpt I reviewed. Ensure Table 1 includes baseline eating window, diet, metformin dose, diabetes duration, and site by arm.
12. Title: The title says "Gut Microbiome Diversity," but the headline taxonomic finding is Akkermansia. Consider aligning the title with the primary outcome once it is designated.
13. Discussion closing sentence: "Promising adjunct to standard care" is reasonable if framed as pilot evidence. Retain the hedging and remove the contradictory causal language elsewhere.
14. Data availability: Deposit raw sequence reads (e.g., SRA/ENA) and provide analysis code.

4. Strengths

• Randomized, parallel-arm design in a clinically relevant T2D population. This is a meaningful step beyond cross-sectional microbiome–insulin resistance associations.
• Homogeneous pharmacological background (stable metformin monotherapy for ≥3 months) and sensible exclusions (antibiotics, pro/prebiotics). Both reduce noise in microbiome outcomes.
• Sound sample handling: OMNIgene-GUT stabilization, −80 °C storage, batch processing, and a standard QIIME2/DADA2/SILVA 138 pipeline.
• Low attrition (3/42) and reported adverse events.
• A candid limitations paragraph in the Discussion. The authors clearly recognize the weight confound, the multiplicity problem, and the absence of ITT and blinding. The revision mainly needs the Abstract and Conclusion to match this candor.
• A pragmatic intervention (ad libitum 8-h window) that is clinically translatable.

5. Recommendation: Major Revision

The study addresses a relevant question with a randomized design and could serve as a useful pilot RCT. The manuscript currently claims more than the data can support, however.

• Claims exceed the design: The mediation language is untested, and weight loss with unmeasured intake prevents attributing effects to meal timing.
• The flagship microbiome result is fragile: The Akkermansia finding is a within-group, uncorrected, species-level claim from V3–V4 16S data.
• Numbers do not reconcile: The reported HbA1c and weight p-values do not match the summary statistics as presented. This must be resolved before the results can be evaluated.
• Trial-reporting essentials are missing: registration, a primary outcome, a power calculation, ITT, and CONSORT.

Many of these problems are fixable with reanalysis and reframing. If the authors resolve the statistical discrepancies, provide ITT and between-group ANCOVA results, apply compositional methods with FDR correction, remove or substantiate the mediation claims, and present the work as a pilot, I would be glad to review a revised version. If the trial was not prospectively registered, or the statistical inconsistencies cannot be reconciled, I would lean toward rejection.