Review Reports - Selective Pharmacological Activation of PPARα/δ/γ Alters the Triglyceride Composition of Fatty Liver in a Diet-Induced MASLD Mouse Model

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Overall the study is well written. The authors performed lipodimics on a diet-induced mouse model of early MASLD. The reviewer notes a few significant issues that need to be addressed.

First, the article is directed at examining changes in lipid content in the liver in response to three different PPAR agonists. In order for this analysis to be useful, some assessment of the degree of PPAR agonist functionality has to be presented. e.g. examination of transcript abundance as a result of PPAR agonist to validate that their function. Likewise, an assesment of their circulating concentration would be useful. Second, a better discussion or perhaps figure, showing how the agonists differ may be useful to help the reader better understand the novelty of comparing the three agonists. Finally, a summary figure would greatly be appreciated.

Author Response

Overall, the study is well written. The authors performed lipidomics on a diet-induced mouse model of early MASLD. The reviewer notes a few significant issues that need to be addressed.

First, the article is directed at examining changes in lipid content in the liver in response to three different PPAR agonists. In order for this analysis to be useful, some assessment of the degree of PPAR agonist functionality has to be presented. e.g. examination of transcript abundance as a result of PPAR agonist to validate that their function. Likewise, an assessment of their circulating concentration would be useful.

We sincerely thank the reviewer for the positive evaluation of our manuscript and for these valuable suggestions.

Regarding the concern about validation of PPAR agonist functionality, we agree that confirmation of pharmacological target engagement is important. We have expanded the Introduction and Discussion to better explain the distinct biological roles and clinical characteristics of PPARα, PPARδ, and PPARγ.

This paper serves as a follow-up to a previous study (old Ref. 7 = new Ref. 10), using the frozen liver samples prepared from the same HFCC/CDX-induced early-stage MASLD mouse model and presenting TG species analysis that was not previously possible and was conducted with the assistance of lipidomics experts in the present study. In the previous study, the blood concentrations achieved without significant changes in body weight ensured the selective activation of PPARα/δ/γ (new Ref. 10). Plasma concentrations of these drugs were measured after 4 weeks treatment, physiologically relevant concentrations of seladelpar and pioglitazone (not pemafibrate) were detected (new Ref. 10). However, the selective activation of PPARα by pemafibrate was demonstrated by the expression of the specific response gene Acox1 in the liver (new Ref. 10). At that time, we were unable to identify genes specifically induced by PPARδ or PPARγ. However, PPARδ activation by seladelpar at doses that do not cause body weight changes has been shown to be effective for the treatment of MASLD only when used in combination with other agents, rather than as a monotherapy (new Ref. 10). PPARγ activation by pioglitazone was most clearly demonstrated by a marked reduction in hepatic TG signal in the present study. We have revised the manuscript to clarify that the dosing regimen provided systemic exposure sufficient for pharmacological activity.

Changes in the manuscript:

Introduction

“While numerous drugs targeting various molecular pathways are currently under development, peroxisome proliferator-activated receptor (PPAR) agonists hold promise for inhibiting the early stages of MASLD—a process progressing from hepatic steatosis to lipotoxicity, inflammation, and fibrosis [2]. PPARs are nuclear receptor transcription factors comprising three subtypes—PPARα, PPARβ/δ, and PPARγ—which differ in their tissue distribution and physiological functions [7]. PPARs play a major role in regulating lipid metabolism: PPARα is mainly expressed in the liver, skeletal muscle, and heart, and induces fatty acid transport and mitochondrial/peroxisomal β-oxidation; PPARδ is expressed in most organs and drives fatty acid oxidation and energy uncoupling [8]; and PPARγ is mainly expressed in adipose tissues, and promotes adipocyte differentiation, fatty acid incorporation, and TG accumulation [9] (new lines 45–56).”

Materials and Methods

“Food intake measurements were performed during PPAR agonist dose setting but were not continuously recorded throughout the entire treatment period in our previous study using the identical HFCC/CDX mouse model [10]. Based on the amount of food consumed, the maximum dose of each PPAR-selective agonist (0.1 mg/kg (body weight)/day for pemafibrate, 1 mg/kg/day for seladelpar, and 3 mg/kg/day for pioglitazone) that could be administered without significant weight changes and could confer selective activation of PPARα/δ/γ was determined [10]. These drugs were mixed into the HFCC feed and were ingested freely with the CDX fluid, achieving pharmacologically relevant blood drug concentrations [10]. Therefore, the present study was conducted using a previously validated fixed-dose regimen rather than a dose-response design (new lines 127–136). ”

Second, a better discussion or perhaps figure, showing how the agonists differ may be useful to help the reader better understand the novelty of comparing the three agonists. Finally, a summary figure would greatly be appreciated.

We agree with the reviewer regarding the need for a clear summary figure.

We have detailed the PPARα/δ/γ selectivity of some PPAR agonists (including these 3 drugs) and their prospects as treatments for NAFLD in our recent (2023) review (new Ref.11, so far cited 69 times), we have deliberately omitted such discussion from this paper.

Furthermore, the downstream signaling pathways of PPARα/δ/γ—even when considering only lipid metabolism—are complex and interconnected, and remain incompletely understood in many respects. Consequently, summarizing them in a single diagram is difficult; papers attempting to do so are rare, and such attempts often lack reliability.

Changes in the manuscript:

Introduction

“PPARs are nuclear receptor transcription factors comprising three subtypes—PPARα, PPARβ/δ, and PPARγ—which differ in their tissue distribution and physiological functions [7]. PPARs play a major role in regulating lipid metabolism: PPARα is mainly expressed in the liver, skeletal muscle, and heart, and induces fatty acid transport and mitochondrial/peroxisomal β-oxidation; PPARδ is expressed in most organs and drives fatty acid oxidation and energy uncoupling [8]; and PPARγ is mainly expressed in adipose tissues, and promotes adipocyte differentiation, fatty acid incorporation, and TG accumulation [9] (new lines 49–56).”

Reviewer 2 Report

Comments and Suggestions for Authors

Hishiki and coworkers use an HFCC/CDX feeding protocol for four weeks and compares pemafibrate, seladelpar, and pioglitazone, followed by LC-MS-based TG profiling to determine whether selective activation of PPARα/δ/γ changes the hepatic triglyceride molecular profile in an early diet-induced MASLD mouse model. The main finding is that the three PPAR agonists have different effects on hepatic TG composition, with pioglitazone reducing the summed TG signal, pemafibrate changing many low-abundance TG species without lowing total hepatic TG signal, and seladelpar showing only modest effects. The work is potentially publishable, but several methodological aspects need to be strengthened before publication. The most important issues are the lack of multiple-testing correction for 225 TG signals, limited quantitative validation of the LC-MS signal as total TG content, insufficient histological quantification, incomplete pharmacodynamic evidence for the three agonists, and some overinterpretation of TG composition changes as mechanistic effects.

The introduction states that the authors previously evaluated the therapeutic effects of pemafibrate, seladelpar, and pioglitazone in the same HFCC/CDX model (page 2, lines 51-65), but could not examine the TG molecular profile in detail at that time. The present study appears to be an extension of that earlier work rather than a fully independent experimental design. Please state clearly whether the liver samples analyzed here were newly generated or derived from the previous animal experiment. If archived samples were used, the authors should add the selection criteria, storage duration, freeze-thaw history, and whether the LC-MS analysis was performed blinded to treatment group.
The doses of pemafibrate, seladelpar, and pioglitazone were selected as the maximum doses that did not cause significant body-weight changes (pages 2-3, lines 83-92), and the compounds were mixed into the HFCC feed for free intake (page 4, lines 141-144). This dosing rationale is not sufficient to compare pharmacological activation across PPARα/δ/γ. Please provide actual food intake per cage, estimated drug intake per mouse, inter-cage variability, and if available, plasma or hepatic drug concentrations. More importantly, the weak seladelpar response may simply reflect inadequate exposure rather than a true biological difference between PPAR subtypes. Therefore, the authors should show target engagement by measuring representative PPAR-responsive genes or proteins, such as Acox1, Cpt1a, or Pdk4 for PPARα; Angptl4 or other PPARδ-responsive markers; and Cd36, or other PPARγ-associated markers.
The manuscript showed that histological examination has no significant changes in lipid accumulation or fibrosis after pemafibrate, seladelpar, or pioglitazone treatment (page 4, lines 139-146). However, the LC-MS data showed that pioglitazone significantly decreased total hepatic TG levels by 44% (page 8, lines 232-235). Please provide quantitative Oil Red O and Sirius Red image analysis, preferably performed blindly, and explain why Oil Red O staining did not detect a clear reduction when the LC-MS total TG signal decreased substantially. Representative images alone are not sufficient for this point.
The extraction protocol describes tissue homogenization in 2-propanol and subsequent LC-MS analysis (page 3, lines 94-103), but no internal standard, recovery control, pooled QC, injection reproducibility, or batch correction procedure is described. Please add these details. If no internal standards were used, the authors should discuss the limitation.
The manuscript reports a more than 5-fold increase in total hepatic TG signal after HFCC/CDX feeding (page 5, lines 172-178) and a 44% decrease after pioglitazone. However, the Methods state that TG proportions were calculated from the sum of peak areas for all detected TG MRM signals (page 3, lines 123-126), and the Discussion notes that absolute quantification was not possible because of the lack of TG standards (page 11, lines 323-326). Please validate the LC-MS-derived total TG signal with an independent biochemical TG assay, or clearly state that “total TG” refers to relative summed LC-MS signal rather than absolute TG mass.
The manuscript should also state whether the cage was considered as an experimental unit or potential random effect, since diet and drug intake were cage-based (page 2, lines 72-81). These details are particularly important because the reported group sizes are modest and some conclusions rely on small changes in relative TG composition.
A major limitation is that the model combines several strong dietary manipulations: high fat, cholesterol, cholic acid, and cyclodextrin (pages 4-5, lines 156-171; page 11, lines 305-306). Without HFCC-only, CDX-only, or high-fat/high-cholesterol without cholic acid controls, it is difficult to determining which component drives the observed TG54 enrichment and the drug-specific TG remodeling. If these control groups are not available, the limitation should be stated explicitly a more prominently in the Discussion.

Author Response

We sincerely thank the reviewer for these valuable suggestions.

The most important issues are the lack of multiple-testing correction for 225 TG signals, limited quantitative validation of the LC-MS signal as total TG content, insufficient histological quantification, incomplete pharmacodynamic evidence for the three agonists, and some overinterpretation of TG composition changes as mechanistic effects.

We thank the reviewer for this helpful comment.

In this paper, since absolute quantification using TG standards was not feasible, the data were treated as peak area signals and were not included in the multiple-testing analysis. Furthermore, the study utilized the same samples prepared in a previous study, where the histology and blood concentration data have already been reported (old Ref. 7 = new Ref. 10). Finally, we have avoided overinterpreting the changes in TG levels, intending to limit the discussion to a straightforward report of the results.

Changes in the manuscript:

Materials and Methods

“The LC–MS analysis was not intended to provide absolute quantification of total hepatic TG content (new lines 179–180).”

Discussion

The introduction states that the authors previously evaluated the therapeutic effects of pemafibrate, seladelpar, and pioglitazone in the same HFCC/CDX model (page 2, lines 51-65), but could not examine the TG molecular profile in detail at that time. The present study appears to be an extension of that earlier work rather than a fully independent experimental design. Please state clearly whether the liver samples analyzed here were newly generated or derived from the previous animal experiment. If archived samples were used, the authors should add the selection criteria, storage duration, freeze-thaw history, and whether the LC-MS analysis was performed blinded to treatment group.

We thank the reviewer for this helpful comment.

We apologize that the relationship between the present study and our previous publication (new Ref. 10) was not sufficiently explained. The liver samples analyzed in the present study were obtained from the same animal experiment reported previously. In the earlier study, we focused on the therapeutic effects of subtype-selective PPAR agonists on the HFCC/CDX-induced MASLD model, whereas comprehensive TG molecular profiling was beyond the scope of that work. The present study therefore represents a new lipidomics analysis using the archived liver samples from the same well-characterized cohort. All liver tissues (small blocks) had been stored continuously at −80°C until lipid extraction, with no repeated freeze–thaw cycles before LC-MS analysis. No selective sampling was performed; liver samples from each experimental group without any selection (n = 9 or 10/group; one pemafibrate sample was accidentally lost due to tube breakage during homogenization using a metal grinder) were included in the lipidomics analysis. Furthermore, the LC-MS measurements and subsequent data processing were conducted using coded samples so that the analytical procedures were performed without knowledge of the treatment groups.

To improve transparency, we have clarified these experimental details in the revised Materials and Methods section.

Changes in the manuscript:

Materials and Methods

“All liver specimens used for lipid analysis were obtained from the same animal experiment reported in our previous study [10]. Livers were quickly removed from isoflurane-anesthetized mice, flash-frozen in liquid nitrogen, and stored at −80°C until lipid extraction without repeated freeze–thaw cycles. Lipid analyses were performed using coded samples to minimize analytical bias with respect to treatment allocation (new lines 144–148).”

The doses of pemafibrate, seladelpar, and pioglitazone were selected as the maximum doses that did not cause significant body-weight changes (pages 2-3, lines 83-92), and the compounds were mixed into the HFCC feed for free intake (page 4, lines 141-144). This dosing rationale is not sufficient to compare pharmacological activation across PPARα/δ/γ. Please provide actual food intake per cage, estimated drug intake per mouse, inter-cage variability, and if available, plasma or hepatic drug concentrations. More importantly, the weak seladelpar response may simply reflect inadequate exposure rather than a true biological difference between PPAR subtypes. Therefore, the authors should show target engagement by measuring representative PPAR-responsive genes or proteins, such as Acox1, Cpt1a, or Pdk4 for PPARα; Angptl4 or other PPARδ-responsive markers; and Cd36, or other PPARγ-associated markers.

We thank the reviewer for this important comment and agree that appropriate pharmacological exposure is essential for interpreting the effects of subtype-selective PPAR agonists.

The doses of pemafibrate, seladelpar, and pioglitazone were selected based on our previous study using the identical HFCC/CDX-induced MASLD mouse model and the same dietary administration protocol (new Ref. 10). During that study, food intake was monitored for dose setting during the treatment period and was used to estimate drug intake. However, food intake was not continuously recorded throughout the entire 4-week treatment period. While the amount of food consumed cannot be measured in standard cages—requiring specialized, expensive equipment instead—it is simply not feasible to measure this for every single mouse. Therefore, we are unable to provide accurate cage-by-cage food consumption or inter-cage variability for the entire experimental period, and we have clarified this point in the revised manuscript.

Importantly, systemic drug exposure was directly confirmed by measuring plasma drug concentrations in our previous study using the identical dosing regimen (new Ref. 10). These pharmacokinetic data demonstrated that all three compounds achieved pharmacologically relevant systemic exposure under the present experimental conditions. We have therefore added a citation to the previous study to clarify that adequate drug exposure was confirmed independently of the estimated food intake.

Regarding pharmacodynamic target engagement, hepatic induction of the representative PPARα target gene Acox1 was confirmed in our previous study under the identical experimental conditions, supporting effective activation of hepatic PPARα signaling (new Ref. 10). Representative PPARδ- and PPARγ-responsive genes were not evaluated in the present study because we failed to find PPARδ- or PPARγ-selectively-responsive genes. We agree that comprehensive assessment of subtype-specific target engagement would further strengthen the interpretation of the lipidomic findings and have acknowledged this limitation in the revised Discussion.

With respect to the relatively modest effect of seladelpar, we agree that inadequate drug exposure should be considered as a possible explanation. However, given that pharmacologically significant plasma concentrations were achieved under the same dosing conditions and some therapeutic effects were observed upon co-administration with other agents (new Ref. 10), we consider it unlikely that insufficient systemic exposure was the primary reason for the limited lipidomic response. Confirmation of subtype-specific target engagement by comprehensive molecular analyses will be an important subject for future investigation.

Changes in the manuscript:

Materials and Methods

Discussion

“As another limitation, while we confirmed the specific induction of Acox1 as evidence of PPARα-selective activation by pemafibrate [10], the similar PPARδ/γ-specific target engagement effects of seladelpar and pioglitazone, respectively, remain to be demonstrated in future studies (new lines 461–464).”

The manuscript showed that histological examination has no significant changes in lipid accumulation or fibrosis after pemafibrate, seladelpar, or pioglitazone treatment (page 4, lines 139-146). However, the LC-MS data showed that pioglitazone significantly decreased total hepatic TG levels by 44% (page 8, lines 232-235). Please provide quantitative Oil Red O and Sirius Red image analysis, preferably performed blindly, and explain why Oil Red O staining did not detect a clear reduction when the LC-MS total TG signal decreased substantially. Representative images alone are not sufficient for this point.

We sincerely thank the reviewer for this valuable comment. We agree that quantitative histological evaluation is important for interpreting the lipidomic findings.

The quantitative analyses of both Oil Red O and Sirius Red staining had been performed in our previous study (new Ref. 10) in a blinded manner for liver sections. These quantitative data demonstrated no statistically significant differences among the treatment groups, consistent with the representative histological images shown in Figure 1 and our previous study (new Ref. 10).

We agree that the apparent discrepancy between the histological findings and the LC–MS results requires further explanation. Oil Red O staining provides a semi-quantitative assessment of neutral lipid accumulation based on the area occupied by lipid droplets in tissue sections, whereas LC–MS quantitatively measures individual TG molecular species extracted from the liver tissue aliquots with substantially higher analytical sensitivity. Consequently, changes in hepatic TG molecular composition or moderate reductions in total TG abundance may not necessarily be accompanied by visually detectable differences in lipid droplet area on histological sections. In the present study, pioglitazone significantly reduced the summed LC–MS TG signal, whereas the overall histological appearance of lipid accumulation remained unchanged. We have added this explanation to the Discussion to clarify the complementary nature of these two analytical approaches and to avoid potential misunderstanding.

Changes in the manuscript:

Discussion

“In our previous study, quantitative analyses of Oil Red O- and Sirius Red-positive areas in the liver sections revealed no statistically significant alteration among the treatment groups (except for reduced fibrosis upon pioglitazone treatment) [10]. Oil Red O staining and LC–MS evaluate different aspects of hepatic lipid accumulation. Oil Red O is a semi-quantitative histological method reflecting lipid droplet area within selected tissue sections, whereas LC–MS provides highly sensitive quantitative measurement of TG molecular species extracted from selected liver aliquots. Therefore, moderate changes in relative total liver TG signal or molecular composition may not necessarily be reflected by detectable differences in histological lipid staining (new lines 441–450).”

The extraction protocol describes tissue homogenization in 2-propanol and subsequent LC-MS analysis (page 3, lines 94-103), but no internal standard, recovery control, pooled QC, injection reproducibility, or batch correction procedure is described. Please add these details. If no internal standards were used, the authors should discuss the limitation.

We sincerely thank the reviewer for this valuable comment regarding the quality control procedures used in the LC–MS analysis.

We have revised the Materials and Methods section to provide additional details regarding analytical quality assurance. No internal standard was used in the present targeted TG analysis because the primary objective was to compare the relative abundance of triglyceride molecular species among experimental groups rather than to perform absolute quantification and all TG standards are not available.

Although pooled QC samples prepared from the study specimens were not included, analytical performance was monitored throughout the measurement sequence using human serum pool analyzed before, during, and after the analytical batch with the same LC–MS panel. These technical QC measurements confirmed that no substantial fluctuation in instrument sensitivity occurred during the analytical run.

Furthermore, all liver samples were extracted using the same protocol and analyzed consecutively under identical LC–MS conditions within a single analytical batch. Therefore, batch correction was considered unnecessary.

We acknowledge that the absence of internal standards represents a limitation of the present study, and this point has now been explicitly stated in the Discussion.

Changes in the manuscript:

Materials and Methods

“No internal standard was used for the present targeted TG analysis. All liver samples were extracted using an identical protocol and analyzed consecutively under identical LC–MS conditions within a single analytical batch. To monitor analytical performance, human serum pool (Cosmo Bio, Tokyo, Japan) was analyzed before, during, and after the analytical batch using the same LC–MS panel. These technical QC measurements confirmed stable instrument performance throughout the analytical sequence. Therefore, batch correction was not performed (new lines 181–187).”

Discussion

“The present lipid analysis was designed to compare the relative abundance of TG molecular species among experimental groups. Because no internal standard was included, absolute correction for extraction efficiency and analytical variability was not possible. Nevertheless, all samples were analyzed under identical experimental conditions within a single analytical batch, and analytical stability was monitored using human serum pool analyzed throughout the measurement sequence. These procedures minimized technical variation; however, the lack of study-specific internal standards should be recognized as a limitation of the present study (new lines 381–388).”

The manuscript reports a more than 5-fold increase in total hepatic TG signal after HFCC/CDX feeding (page 5, lines 172-178) and a 44% decrease after pioglitazone. However, the Methods state that TG proportions were calculated from the sum of peak areas for all detected TG MRM signals (page 3, lines 123-126), and the Discussion notes that absolute quantification was not possible because of the lack of TG standards (page 11, lines 323-326). Please validate the LC-MS-derived total TG signal with an independent biochemical TG assay, or clearly state that “total TG” refers to relative summed LC-MS signal rather than absolute TG mass.

We sincerely thank the reviewer for this valuable comment. We agree that the terminology used to describe the LC-MS results should more clearly distinguish relative lipidomic signals from absolute TG mass.

As pointed out by the reviewer, the present lipidomic analysis was based on the summed peak areas of all detected TG MRM signals. Because authentic standards for all detected TG molecular species were not available, the LC–MS analysis was designed to provide relative quantitative comparisons among experimental groups rather than absolute quantification of hepatic TG content. Therefore, the term “total hepatic TG (level)” used in the original manuscript may lead to misunderstanding.

Accordingly, we have revised the manuscript throughout to replace expressions such as “total hepatic TG (level)” with “summed TG LC–MS signal” or “relative total TG signal”, as appropriate. We have also clarified in the Materials and Methods and Discussion that the summed LC–MS signal reflects the relative abundance of the detected TG molecular species rather than the absolute hepatic TG mass.

Biochemical quantification of total hepatic TG would provide complementary information. In our previous study {Honda, 2026 #150}, we performed a biochemical quantification of total hepatic triglyceride (TG) content using a standard colorimetric kit, but observed no changes among the treatment groups. This kit quantifies the amount of free glycerol released from TGs; consequently, it could not distinguish between TGs, diacylglycerols, monoacylglycerols, and glycerol itself. Therefore, it is not surprising that measurement results vary with LC-MS method.

Changes in the manuscript:

Whole manuscript

All “total (hepatic) TG (level)” was replaced with “ summed (liver) TG LC-MS signals” or “relative total (liver) TG signals.

Materials and Methods:

“The TG carbon-number group signals were calculated as the sum of the MRM signals with the identical Q1 transition. The proportion of each TG type was expressed as parts per million (ppm) of the relative total TG signals (the sum of peak areas for all TG MRM signals). The LC–MS analysis was not intended to provide absolute quantification of total hepatic TG content (new lines 176-180).”

The manuscript should also state whether the cage was considered as an experimental unit or potential random effect, since diet and drug intake were cage-based (page 2, lines 72-81). These details are particularly important because the reported group sizes are modest and some conclusions rely on small changes in relative TG composition.

We sincerely thank the reviewer for this important comment regarding the experimental unit and the potential influence of cage effects.

In the present study, mice were randomly assigned to cages before initiation of the dietary intervention, with five mice housed per cage (two cages per treatment group). Although the experimental diets containing each PPAR agonist were provided on a cage basis, all biological endpoints, including histological evaluation and LC–MS lipidomic analyses, were obtained independently from individual liver samples. Therefore, the individual mouse was considered the experimental unit for all statistical analyses (n = 9 or 10 per group).

We acknowledge that dietary administration inherently introduces the possibility of cage-related effects on food consumption. However, all groups were maintained under identical housing conditions, cage assignments were randomized, and no apparent cage-specific differences in general condition during the study. Accordingly, cage was not incorporated as a random effect in the statistical analyses. To improve transparency, we have clarified the housing conditions, cage allocation, and statistical unit in the revised Materials and Methods.

Changes in the manuscript:

Materials and Methods

“Mice were randomly allocated to cages before treatment (five mice per cage; two cages per experimental group). Although medicated diets were supplied on a cage basis, all histological and lipid analyses were performed using independently collected liver samples from individual animals. Therefore, the individual mouse was considered the experimental unit for all statistical analyses (new lines 137–141).”

A major limitation is that the model combines several strong dietary manipulations: high fat, cholesterol, cholic acid, and cyclodextrin (pages 4-5, lines 156-171; page 11, lines 305-306). Without HFCC-only, CDX-only, or high-fat/high-cholesterol without cholic acid controls, it is difficult to determining which component drives the observed TG54 enrichment and the drug-specific TG remodeling. If these control groups are not available, the limitation should be stated explicitly a more prominently in the Discussion.

We sincerely thank the reviewer for this thoughtful comment.

We agree that the HFCC/CDX model incorporates multiple dietary components, including high fat, cholesterol, cholic acid, and cyclodextrin, each of which may contribute differently to hepatic lipid remodeling. However, the primary objective of the present study was not to dissect the individual contribution of each dietary component in a commercially available diet, but rather to comprehensively characterize TG molecular profiles and their responses to subtype-selective PPAR agonists using a well-established early-stage MASLD model. Accordingly, separate control groups receiving HFCC alone, CDX alone, or modified diets lacking individual components were not included in the experimental design.

We agree that, in the absence of these additional dietary control groups, it is not possible to determine which specific dietary component(s) are primarily responsible for the enrichment of TG54 species or the distinct TG remodeling induced by each PPAR agonist. We have therefore revised the Discussion to explicitly acknowledge this limitation and to emphasize that future studies employing simplified dietary models or systematic dietary component comparisons will be necessary to clarify the individual contributions of each dietary factor.

We believe this revision more appropriately defines the scope of the present study and avoids overinterpretation of the observed lipid changes.

Changes in the manuscript:

Discussion:

“The HFCC/CDX model combines several dietary factors, including high fat, cholesterol, cholic acid, and cyclodextrin, each of which may influence hepatic lipid metabolism. Because the present study used the commercially available diet and did not include control groups lacking individual dietary components, the specific contribution of each component to TG54 enrichment or drug-induced TG remodeling cannot be determined. Future studies using simplified dietary models or systematic comparisons of individual dietary components will be required to clarify the respective roles of these dietary factors (new lines 329–336).”

Reviewer 3 Report

Comments and Suggestions for Authors

The authors present an interesting and innovative manuscript regarding the role of various PPAR agonists in triglyceride accumulation in mouse models.

The introduction section is too small. The authors try different PPAR agonists and try to see the impact on triglyceride accumulation in the liver. They should explain the pathophysiology of PPAR agonism in lipid metabolism and why they used these drugs. Was it just because these were available t.ex.? what did the authors expect based on differnet PPARs. What is the difference between drugs used? What is the purpose of the study? Since no great MASLD mouse model exists these study should show differences in different PPAR agonism and potentially interaction between different PPARs
In materials and methods I would like to know how the dosage of each drug was found. If the authors performed some expereminets these should be adequately explained in methods section. Likewise, if they used previous experience from other studies they should clearly explain that. Otherwise, one could think that the results were dose-dependent
I think the results section is well written, as the authors show all available data for each drug. The authors show the results regarding total cholesterol as well as the lipidemic profile. Moreover, this part is written in a professional and simple manner so that the reader can easily understand the authors' findings
The discussion part also needs vast improvement. The part on why this diet was used should be transferred to materials and methods. In results the authors should talk about their findings. Likewise, in a manuscript using mouse models, the discussion of possible approval and phase 2/3 trials in human for the drugs used in the study is unnecessary. The meaning of a "mouse" experiment is understanding the pathophysiology, not determing the suitability of each drug for human.
On the same note, even though the authors begin trying to explain their findings based on pathophysiological pathways talk too much about the success or no success of each drug in their human experiments. I would suggest trying to elucidate why did different PPAR agonism led to different lipiodomic profile and if a certain PPAR agonism should be better exploited.

Author Response

The authors present an interesting and innovative manuscript regarding the role of various PPAR agonists in triglyceride accumulation in mouse models.

We sincerely thank the reviewer for the positive evaluation of our manuscript and for these valuable suggestions.

The introduction section is too small. The authors try different PPAR agonists and try to see the impact on triglyceride accumulation in the liver. They should explain the pathophysiology of PPAR agonism in lipid metabolism and why they used these drugs. Was it just because these were available? what did the authors expect based on different PPARs. What is the difference between drugs used? What is the purpose of the study? Since no great MASLD mouse model exists, this study should show differences in different PPAR agonism and potentially interaction between different PPARs

We sincerely thank the reviewer for this constructive comment.

We agree that the Introduction was too concise and did not sufficiently describe the physiological roles of PPAR subtypes in lipid metabolism, nor clearly explain the rationale for selecting the three PPAR agonists used in this study. Such information has already been addressed in our recent papers, and we had hoped to avoid redundancy. However, we have come to realize that this paper stands on its own and that the content cannot be fully understood without including this additional explanation.

In the revised manuscript, we have substantially expanded the Introduction to better describe the pathophysiological roles of PPARα, PPARδ, and PPARγ in hepatic lipid metabolism and their distinct regulatory functions in fatty acid oxidation, lipid transport, and lipid storage. We also clarified the rationale for selecting pemafibrate, seladelpar, and pioglitazone, which represent clinically relevant and subtype-selective agonists targeting PPARα/δ/γ, respectively.

Importantly, we have now explicitly stated the hypothesis of this study: that differential activation of PPAR subtypes may lead to distinct remodeling of hepatic TG molecular species in early-stage MASLD. We further clarified that the purpose of the study was not simply to test available compounds, but to systematically compare subtype-selective PPAR activation in a well-established diet-induced MASLD model. We believe these changes significantly improve the clarity and scientific framing of the study.

Changes in the manuscript:

Introduction:

“In a previous study [10], we used an early-stage mouse model of MASLD to systematically investigate the therapeutic effects of activating PPARα/δ/γ using clinically relevant drugs—specifically, agents that are already approved with established safety profiles or those currently undergoing clinical trials for MASLD. The agents employed were pemafibrate, seladelpar, and pioglitazone, which are selective agonists for PPARα/δ/γ, respectively [11] (new lines 57–62).”

“Through such research, we hypothesized that the three PPAR subtypes might induce distinct patterns of TG accumulation in the fatty liver of this early-stage MASLD mouse model. The objective of this study was to systematically compare the effects of PPARα/δ/γ activation on the molecular remodeling of TG by performing lipid analysis using liquid chromatography-mass spectrometry (LC–MS) on frozen liver samples prepared in our previous study [10] (new lines 75–80).”

In materials and methods, I would like to know how the dosage of each drug was found. If the authors performed some experiments, these should be adequately explained in methods section. Likewise, if they used previous experience from other studies, they should clearly explain that. Otherwise, one could think that the results were dose-dependent.

We sincerely thank the reviewer for this important comment regarding the rationale for dose selection.

The doses of pemafibrate, seladelpar, and pioglitazone used in the present study were not arbitrarily chosen but were based on our previously published work using the identical HFCC/CDX-induced MASLD mouse model and the same dietary administration protocol. In that study, we systematically evaluated the therapeutic effects of these PPAR agonists and confirmed that the selected doses did not induce significant changes in body weight while maintaining pharmacologically relevant exposure.

Importantly, dose selection was guided by two key considerations: (1) avoidance of confounding effects due to drug-induced alterations in food intake or body weight, and (2) previously confirmed systemic exposure levels. In our earlier study, estimated food/drug intake per mouse were assessed, and plasma drug concentrations were measured, demonstrating that the selected dosing regimens achieved pharmacologically active systemic exposure for all three compounds.

Therefore, the present study represents a targeted lipidomics analysis using a previously validated dosing regimen, rather than a dose-finding or dose-response study. We have clarified this rationale in the revised Materials and Methods section to avoid misunderstanding that the observed effects are driven by dose dependency.

Changes in the manuscript:

Materials and Methods

I think the results section is well written, as the authors show all available data for each drug. The authors show the results regarding total cholesterol as well as the lipidemic profile. Moreover, this part is written in a professional and simple manner so that the reader can easily understand the authors' findings.

Although of interest, “cholesterol” molecular species were not measured/investigated in this analysis.

The discussion part also needs vast improvement. The part on why this diet was used should be transferred to materials and methods. In results the authors should talk about their findings. Likewise, in a manuscript using mouse models, the discussion of possible approval and phase 2/3 trials in human for the drugs used in the study is unnecessary. The meaning of a "mouse" experiment is understanding the pathophysiology, not determining the suitability of each drug for human.

We have moved the explanation of why this diet was adopted to the Materials and Methods. We have omitted the mention of semaglutide and resmetirom having been recently approved from the Discussion section, but we have retained the references to PPAR agonists currently undergoing clinical trials for MASLD. All three drugs in this paper are either currently in clinical trials for MASLD or expected to see a resumption of such trials; consequently, studies investigating their effects on the liver—even those involving animal models—are highly relevant. Indeed, we believe many researchers are interested in this aspect for precisely that reason.

Changes in the manuscript:

Materials and Methods

The explanation of why this diet was adopted has been moved to Materials and Methods (new lines 106–124).

Discussion

The two original sentences “Although various drugs have been developed to treat MASLD, only two have been approved [4]. Resmetirom (a thyroid hormone receptor beta-selective agonist) was approved in April 2024 following the results of the MAESTRO-NASH trial (NCT03900429) [18]. More recently, semaglutide (a glucagon-like peptide-1 receptor agonist) was approved in August 2025 following the results of the ESSENCE trial (NCT04822181) [19] (old lines 287–291)” have been deleted.

“Meanwhile, clinical trials involving seladelpar for NAFLD/NASH patients are currently suspended whereas trials involving pioglitazone have been ongoing for a decade [11] (new lines 344–346).”

Conclusion

“All three drugs are either currently in clinical trials for MASLD or expected to see a resumption of such trials [11]; consequently, studies investigating their effects on the liver—even those involving animal models—are highly relevant (new lines 467–470).”

On the same note, even though the authors begin trying to explain their findings based on pathophysiological pathways talk too much about the success or no success of each drug in their human experiments. I would suggest trying to elucidate why did different PPAR agonism led to different lipidomic profile and if a certain PPAR agonism should be better exploited.

We have now clearly noted in the Introduction that “The objective of this study was to systematically compare the effects of PPARα/δ/γ activation on the molecular remodeling of TG (new lines 77–78)” and found some alteration among the treatment group. However, as we mentioned as the limitation of this study, the relationship between the observed changes in TG composition and the pathology/improvement of fatty liver in the MASLD model remains completely unknown (old lines 392–394 = new lines 451–453).

The downstream signaling pathways of PPARα/δ/γ—even when considering only lipid metabolism—are complex and interconnected, and remain incompletely understood in many respects. Unfortunately, even when combined with the results of our previous study (new Ref. 10), no conclusion has been reached regarding which treatment is best. Nevertheless, all three drugs in this paper are either currently in clinical trials for MASLD or expected to see a resumption of such trials; consequently, studies investigating their effects on the liver—even those involving animal models—are highly relevant.

Changes in the manuscript:

Discussion

“Meanwhile, clinical trials involving seladelpar for NAFLD/NASH patients are currently suspended whereas trials involving pioglitazone have been ongoing for a decade [11] (new lines 344–346).”