Diet-conditioned microbiota enhances fecal microbiota transplantation efficacy in alcoholic liver disease through caproic acid-PPARα signaling

Reviewer #1 (Public review):

Summary:

The authors aimed to determine whether dietary conditioning of fecal microbiota donors can influence the therapeutic efficacy of fecal microbiota transplantation (FMT) in alcohol-associated liver disease (ALD). Specifically, they tested whether donor diets enriched in vegetable or egg-derived proteins alter microbiota composition and function in ways that enhance recovery from alcohol-induced liver injury. Using a murine ALD model, the study integrates microbiome profiling, metabolomics, proteomics, and functional assays to identify mechanisms underlying improved outcomes. The authors propose that vegetable protein-conditioned microbiota promote beneficial microbial remodeling and increased production of caproic acid, which in turn activates hepatic PPARα signaling and enhances fatty acid β-oxidation, thereby reducing steatosis and inflammation.

Strengths:

The study is ambitious and methodologically comprehensive. The central idea, that donor diet can modulate FMT efficacy in ALD, is compelling and potentially impactful. It combines in vivo disease models, microbiome analysis (16S rRNA sequencing), metabolomics and proteomics, pharmacological inhibition experiments, and in vitro validation in hepatocytes. This multi-layered approach is a clear strength and allows the authors to explore the gut-liver axis. The comparison between different protein sources (vegetable vs egg) is very interesting, and the PPARα inhibition experiments provide relatively strong functional support for the involvement of host metabolic signaling pathways in mediating the observed effects.

Weaknesses:

Despite the comprehensive scope of the manuscript, several aspects of the study limit the strength of its mechanistic conclusions. The causal attribution to caproic acid remains incomplete. While caproic acid is identified and functionally tested, there is no direct demonstration that it is necessary for the Veg-FMT phenotype in vivo. The metabolomics data suggest multiple candidate metabolites, but these are not systematically explored. The study identifies specific bacterial taxa and, separately, key metabolites, but does not establish a direct connection between microbial composition and metabolite production. The use of GW6471 supports involvement of PPARα but does not fully establish specificity, as off-target effects cannot be excluded. Finally, it is not fully clear whether effects are exclusively microbiota-driven or could partially reflect the transfer of diet-derived metabolites.

The authors successfully demonstrate that donor dietary conditioning influences the therapeutic efficacy of FMT in a murine model of ALD. The data convincingly show that vegetable protein-conditioned microbiota is associated with improved liver injury, reduced inflammation, and enhanced intestinal barrier integrity compared with controls or an egg protein-enriched diet. While the proteomic and gene expression data suggest activation of pathways related to fatty acid β-oxidation, these measurements do not directly demonstrate increased metabolic flux. The use of the PPARα antagonist GW6471 provides important functional support for the involvement of this pathway, as inhibition attenuates the protective effects of Veg-FMT. However, this approach primarily establishes pathway dependency rather than directly confirming enhanced β-oxidation activity. The authors may therefore wish to moderate their interpretation or clarify this distinction, particularly given the relatively modest fold changes observed in several targets. The role of caproic acid as a central mediator is plausible but not definitively established. Finally, the link between microbiota composition, metabolic function, and host signaling remains partly correlative. Overall, the study achieves its primary aim at a phenotypic level, but some of the mechanistic claims would benefit from more cautious interpretation or additional validation.

Likely impact of the work on the field, and the utility of the methods and data to the community:

The work addresses an important and underexplored question: how donor characteristics influence FMT efficacy. By introducing donor diet as a modifiable variable, the study has potential implications for optimizing microbiota-based therapies. The datasets (microbiome, metabolomics, and proteomics) may also be valuable to the community, as they provide a resource for exploring gut-liver metabolic interactions. The translational impact will, however, depend on validation in human systems and a clearer identification of causal mechanisms.

Reviewer #2 (Public review):

The manuscript explores a valuable strategy for optimizing Fecal Microbiota Transplantation (FMT) efficacy in alcoholic liver disease through donor dietary intervention. I have identified several critical logical gaps, missing links in the evidence chain, and methodological ambiguities that require detailed explanation and supplementation.

(1) While the Methods section states that each recipient mouse group consisted of 16 animals, microbiome sequencing was performed on only 4 samples per group. This sample size is insufficient, and the high inter-individual variability observed reduces the statistical power and representativeness of the data. I recommend increasing the sequencing sample size or, at a minimum, explicitly acknowledging the risk of false positives due to the small sample size in the Discussion.

(2) The layout of Figure 4 should be adjusted. Panel A should be enlarged for better visibility, while Panel B should be reduced in size to balance the figure composition.

(3) A rationale should be provided for the selection of egg white protein as the animal protein control. Does this adequately represent animal proteins in general? Could the results differ if casein or whey protein were used? The current choice limits the generalizability of the conclusions, and this limitation should be addressed.

(4) The ALD model was established over 12 weeks, yet the FMT intervention consisted of only 3 administrations with a 1-week observation period. In the context of such a severe liver injury model, a 1-week recovery period appears insufficient to observe genuine fibrosis reversal, which typically requires a longer timeframe. The authors should discuss whether short-term FMT can truly induce structural remodeling or if the observed effects are transient.

(5) The results rely heavily on PICRUSt2 for functional prediction. As prediction does not equate to factual validation, the authors should exercise caution in their wording within the Discussion. Alternatively, I recommend supplementing the study with shotgun metagenomic sequencing to verify the existence of these pathways rather than relying solely on predictive algorithms.

(6) Although Egg-FMT was less effective than Veg-FMT, it performed better than the standard FMT or abstinence groups. Why is the effect of egg white protein intermediate? Is this due to rapid digestion resulting in insufficient substrate, or differences in metabolite production? A deeper comparative analysis of the Egg-FMT group is required, rather than treating it merely as a negative control.

(7) Relying solely on the "inhibitor blocking effect" proves only that Caproic acid's function is dependent on the PPARα pathway, not that it directly acts on PPARα. To claim direct activation, the authors must demonstrate direct binding between Caproic acid and the PPARα protein (e.g., via SPR or MST assays). Alternatively, a luciferase reporter assay driven specifically by PPARα response elements (PPRE) should be conducted. If Caproic acid induces luminescence, it would confirm transcriptional activation of PPARα rather than mere downstream activation.

Author response:

We thank the Reviewing Editor, Senior Editor, and both reviewers for their constructive evaluation of our manuscript. We are encouraged that the reviewers found the central question, whether donor dietary conditioning modulates FMT efficacy in ALD, compelling and the multi-omics framework a strength. Their critiques converge on a shared theme: the manuscript's mechanistic claims around caproic acid and PPARα signaling currently rest on associative and pathway-level evidence, and would benefit from more direct causal testing and more guarded language. We agree, and we outline below the revisions we plan to undertake.

Public Reviews:

Reviewer #1 (Public review):

While the proteomic and gene expression data suggest activation of pathways related to fatty acid β-oxidation, these measurements do not directly demonstrate increased metabolic flux. The use of the PPARα antagonist GW6471 provides important functional support for the involvement of this pathway; however, this approach primarily establishes pathway dependency rather than directly confirming enhanced β-oxidation activity. The role of caproic acid as a central mediator is plausible but not definitively established. Finally, the link between microbiota composition, metabolic function, and host signaling remains partly correlative.

We thank the reviewer for this thoughtful assessment. We agree that the GW6471 inhibition experiments primarily support pathway dependency rather than direct activation of PPARα by caproic acid, and we will revise the manuscript accordingly to avoid overstating mechanistic conclusions. However, we would like to clarify that the objective of the current study was not to directly quantify metabolic flux. We agree that metabolic flux should not be used here. We will be modifying this in the text to make it clear that we measured mitochondrial beta oxidation as a response to caproic acid.

To functionally assess alterations in fatty acid β-oxidation capacity, we performed Seahorse Mito Fuel Flex assays, which demonstrated altered dependency and utilization of fatty acid oxidation pathways in response to caproic acid treatment. We will further clarify this distinction in the revised.

In addition, we agree that the role of caproic acid as a central mediator and the relationship between microbiota composition, metabolite production, and host signaling remain partly correlative. Therefore, we will moderate the interpretation throughout the manuscript and incorporate additional correlation analyses between microbial taxa, caproic acid levels, and disease-associated metabolic parameters to strengthen the microbiota-metabolite-host association while acknowledging the associative nature of these findings.

Reviewer #2 (Public review):

(1) While the Methods section states that each recipient mouse group consisted of 16 animals, microbiome sequencing was performed on only 4 samples per group. This sample size is insufficient, and the high inter-individual variability observed reduces the statistical power and representativeness of the data. I recommend increasing the sequencing sample size or, at a minimum, explicitly acknowledging the risk of false positives due to the small sample size in the Discussion.

We thank the reviewer for this important comment. We would like to clarify that microbiome sequencing was performed on 6 samples per group and not on 4 samples per group, and we will revise the Methods section to improve clarity regarding the number of biological replicates analyzed. The 4 samples were used only for whole proteome analysis.

In addition, several previously published murine microbiome studies investigating gut microbial alterations in liver disease and FMT interventions have used comparable sample sizes (typically 5-8 animals per group) for 16S rRNA sequencing analyses [1–3]. Nevertheless, we agree that inter individual variability may influence microbiome analyses, and therefore we will explicitly acknowledge this limitation and the possibility of reduced statistical power in the revised Discussion section. We will also ensure that interpretations derived from microbiome compositional analyses are presented more cautiously.

(2) The layout of Figure 4 should be adjusted. Panel A should be enlarged for better visibility, while Panel B should be reduced in size to balance the figure composition.

We thank the reviewer for this suggestion. We will revise the layout of Figure 4 accordingly by enlarging Panel A for improved visibility and reducing the size of Panel B to achieve a more balanced figure composition.

(3) A rationale should be provided for the selection of egg white protein as the animal protein control. Does this adequately represent animal proteins in general? Could the results differ if casein or whey protein were used? The current choice limits the generalizability of the conclusions, and this limitation should be addressed.

We thank the reviewer for this important suggestion. In the revised manuscript, we will provide additional rationale for selecting egg albumin as the animal-derived protein source. Egg albumin was chosen because it is a well-characterized protein with high biological value, rapid digestibility, standardized composition, and has also been used in our previous ALD-related dietary intervention studies for experimental consistency [4].

We agree that egg albumin does not represent all animal protein sources. Due to its rapid digestion and absorption, relatively less substrate may reach the distal gut for microbial fermentation compared with more complex proteins. In contrast, proteins such as casein or whey may generate distinct microbial and metabolite profiles and potentially different host responses.

Accordingly, we will explicitly acknowledge this limitation in the revised manuscript and clarify that our findings should not be generalized to all animal-derived proteins.

(4) The ALD model was established over 12 weeks, yet the FMT intervention consisted of only 3 administrations with a 1-week observation period. In the context of such a severe liver injury model, a 1-week recovery period appears insufficient to observe genuine fibrosis reversal, which typically requires a longer timeframe. The authors should discuss whether short-term FMT can truly induce structural remodeling or if the observed effects are transient.

We thank the reviewer for this important and thoughtful observation. We agree that a one-week post-FMT observation period appears insufficient to conclude complete structural remodeling or durable fibrosis reversal in a chronic 12-week ALD model. Though it should be noted that the results achieved with the one week intervention suggest otherwise in this animal model of ALD. As can be observed from the immunohistochemistry of abstinence and treatment groups, which was further quantified for steatosis and fibrosis, there is a __% and __% reduction respectively in the treatment group. Thus we can safely conclude that in the given animal model, an alternate day FMT for 3 doses can reverse steatosis and fibrosis.

In the revised manuscript, we will explicitly clarify this distinction.

(5) The results rely heavily on PICRUSt2 for functional prediction. As prediction does not equate to factual validation, the authors should exercise caution in their wording within the Discussion. Alternatively, I recommend supplementing the study with shotgun metagenomic sequencing to verify the existence of these pathways rather than relying solely on predictive algorithms.

We thank the reviewer for this important suggestion and agree that PICRUSt2-based analyses represent predictive functional inference rather than direct validation of microbial metabolic activity. We will explicitly acknowledge in the Results and Discussion that PICRUSt2 outputs are inferences rather than measurements, and we will integrate our metabolomics data to show where predicted microbial pathways (fatty acid salvage, β-oxidation related pathways) coincide with measurable metabolite shifts, providing observational support for the predictions.

We would like to avoid doing metagenomic analysis to substantiate PICRUST2 findings primarily because metagenomic analysis would provide information on the set of genes each species carries, and not the functional state of the resulting pathways. To read out the pathways we would be left with the same two options of PICRUS2 or metabolome analysis. Yes, if we perform transcriptome analysis we can reach to a conclusion on which pathways are active. Which is likely to be similar to the readout we get from the end result of these pathways – the metabolome.

(6) Although Egg-FMT was less effective than Veg-FMT, it performed better than the standard FMT or abstinence groups. Why is the effect of egg white protein intermediate? Is this due to rapid digestion resulting in insufficient substrate, or differences in metabolite production? A deeper comparative analysis of the Egg-FMT group is required, rather than treating it merely as a negative control.

We thank the reviewer for this insightful observation. We agree that the Egg-FMT group demonstrated an intermediate phenotype and should not be interpreted merely as a negative control. We will modify the text in the manuscript to mention the outcomes with egg protein, wherever it missing. In the revised manuscript, we will modify the language accordingly and expand the Discussion.

(7) “Relying solely on the ‘inhibitor blocking effect’ proves only that Caproic acid's function is dependent on the PPARα pathway, not that it directly acts on PPARα. To claim direct activation, the authors must demonstrate direct binding between Caproic acid and the PPARα protein (e.g., via SPR or MST assays). Alternatively, a luciferase reporter assay driven specifically by PPARα response elements (PPRE) should be conducted. If Caproic acid induces luminescence, it would confirm transcriptional activation of PPARα rather than mere downstream activation.”

We thank the reviewer for this important and insightful suggestion. We agree that the current inhibitor-based experiments primarily support the involvement of the PPARα pathway and do not definitively establish direct interaction or transcriptional activation of PPARα by caproic acid. Accordingly, in the revised manuscript, we will moderate our interpretation and avoid statements implying direct activation based solely on the current data.

We also agree that direct validation experiments such as SPR/MST-based binding assays or PPREdriven luciferase reporter assays would substantially strengthen the mechanistic conclusions. We are currently planning additional experiments to further evaluate the direct action of caproic acid on PPARα and will incorporate these analyses in future revisions and follow-up studies.

With the pending experiments we request the Editors to kindly provide us a time of about 2 months to send back the revised manuscript.

References:

(1) Mitsinikos, F. T., Chac, D., Schillingford, N. & DePaolo, R. W. Modifying macronutrients is superior to microbiome transplantation in treating nonalcoholic fatty liver disease. Gut Microbes 12, 1792256.

(2) Ferrere, G. et al. Fecal microbiota manipulation prevents dysbiosis and alcohol-induced liver injury in mice. J. Hepatol. 66, 806–815 (2017).

(3) Zhang, Y., Li, P., Chen, B. & Zheng, R. Therapeutic effects of fecal microbial transplantation on alcoholic liver injury in rat models. Clin. Res. Hepatol. Gastroenterol. 48, 102478 (2024).

(4) Mittal, A. et al. Protein supplementation differentially alters gut microbiota and associated liver injury recovery in mouse model of alcohol-related liver disease. Clin. Nutr. 46, 96–106 (2025).