Review Reports - Divergent Effects of Palm Tocotrienol-Rich Mixture in Refined Olive Oil and Alpha-Tocopherol on Joint Health in a Rat Model of Osteoarthritis Induced with Monosodium Iodoacetate

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The manuscript states that PT attenuated the negative time-dependent changes in joint width and grip strength; however, the mixed-design ANOVA showed no significant treatment effect for joint width, and the manuscript mainly reports an absence of significant within-group temporal change in the PT group. For grip strength, a significant treatment effect was observed, but the clearly reported week-4 difference was between GS and the OA control. Therefore, statements describing PT as “attenuating” these functional/time-dependent changes, particularly in the Abstract, should be softened or explicitly supported by the relevant treatment × time comparisons.
Please report and discuss the treatment × time interaction for the longitudinal outcomes. This is particularly relevant for grip strength because Table S1 reports a significant treatment × time interaction (p=0.0433), whereas the Results section focuses primarily on the separate treatment and time effects. The interaction is arguably the most informative statistic for determining whether the trajectories differed among treatment groups and should therefore be explicitly reported in Section 2.1 and, where appropriate, followed by clearly described post-hoc comparisons.
There appears to be an inconsistency between the main text and Supplementary Table S1 regarding phosphorylated NF-κB. Section 2.4 states that no significant difference in phosphorylated NF-κB was detected across groups, whereas Table S1 reports a significant overall Kruskal–Wallis result for p-NFκB (H=14.67, p=0.0054), with the note that Dunn’s post-hoc comparisons did not identify significant pairwise differences. The Results should distinguish between a significant omnibus test and the absence of significant post-hoc pairwise comparisons rather than describing the parameter simply as showing “no significant difference.”
The interpretation of the histological findings for PT should remain restricted to the structural component of the Mankin score. PT significantly reduced the structural score compared with the OA control, but did not significantly improve the cellular, matrix, tidemark, or total Mankin scores. Thus, wording such as “reduced cartilage structural damage” is appropriate, whereas broader statements implying overall histological protection should be avoided. This distinction is particularly important because GS, unlike PT, significantly improved the structural, cellular, and total scores.
The authors should clarify the nomenclature of the Wnt target measured by qRT-PCR. The Methods and Results repeatedly refer to “Wnt” expression, while Table 2 identifies the primer specifically as Wnt3a. The manuscript and Figure 4 should consistently report Wnt3a if this is the transcript that was actually quantified. This is important because “Wnt” refers to a family of ligands rather than a single gene.
The vehicle difference between PT and the remaining groups deserves slightly clearer treatment in the interpretation of the PT effect. PT was diluted in refined olive oil, whereas the normal control, OA control, AT, and GS groups received distilled-water-based preparations. The authors appropriately acknowledge this limitation, but because there was no olive-oil vehicle control, the observed PT effect cannot be unequivocally attributed to the tocotrienol-rich mixture alone. I suggest explicitly stating this point when interpreting the PT-versus-OA comparisons, rather than restricting it to the limitations paragraph.
The discussion of the AT findings should avoid implying structural worsening beyond what was directly demonstrated. The molecular findings for AT are interesting, particularly the increases in Il1b, Mmp13, Sost, and Ctnnb-related measures; nevertheless, the manuscript itself notes that clear evidence of structural worsening was not demonstrated. Moreover, the principal histological comparisons reported for AT are against the GS group rather than showing a significant worsening relative to the OA control. Statements such as “AT causes more severe damage” should therefore be revised to wording such as “AT was associated with a more catabolic molecular/transcriptional profile under the present experimental conditions.”
Please clarify the interpretation of serum COMP, particularly the OA+AT versus OA+GS difference. The only reported significant COMP comparison was a lower value in the AT group than in the GS group, while no other between-group differences were detected. The subsequent suggestion that lower COMP in AT-treated animals might indicate insufficient ECM synthesis is explicitly speculative and is not supported by additional synthesis/degradation biomarkers in this experiment. I recommend shortening this interpretation and making clear that the COMP data do not independently support a detrimental effect of AT.
The authors should provide a little more methodological detail for the qRT-PCR quality-control procedure. The manuscript reports RNA concentration/optical purity and use of the 2^-ΔΔCt method with Gapdh, but does not indicate whether amplification specificity (e.g., melting-curve analysis), primer efficiency, and technical replicate measurements were assessed. Given that several central conclusions are based on relatively selective transcript-level changes (particularly Il1b, Mmp13, Sost, and Ctnnb), these details would improve reproducibility without requiring additional experiments.
The final translational statement regarding PT as an adjunct or alternative intervention should be moderated. The present study is a four-week MIA rat experiment with n=6/group, and the authors themselves acknowledge that inflammatory changes may have subsided by the sampling point, that treatment/grip-strength assessment was unblinded, and that the AT dose has limited translational comparability. Accordingly, the statement that PT “may serve as a therapeutic adjunct or an alternative intervention for patients with OA who are unsuitable for conventional GS treatment” goes somewhat beyond the current evidence. It would be more appropriate to conclude that the findings support further preclinical evaluation of PT, including its potential combination with GS, before making a patient-oriented therapeutic positioning.

Author Response

Dear reviewer,

Thank you for your meticulous review. Your constructive comments have been carefully considered and replied in the attached response sheet. We thank you for your time in reviewing this submission again and hope the revised version can meet the standards of the journal.

Reviewer 1

Title: Divergent Effects of Palm Tocotrienol-Rich Mixture and Alpha-Tocopherol on Joint Health in a Rat Model of Osteoarthritis Induced with Monosodium Iodoacetate

ID: pharmaceuticals-4548459

Comment

The manuscript states that PT attenuated the negative time-dependent changes in joint width and grip strength; however, the mixed-design ANOVA showed no significant treatment effect for joint width, and the manuscript mainly reports an absence of significant within-group temporal change in the PT group. For grip strength, a significant treatment effect was observed, but the clearly reported week-4 difference was between GS and the OA control. Therefore, statements describing PT as “attenuating” these functional/time-dependent changes, particularly in the Abstract, should be softened or explicitly supported by the relevant treatment × time comparisons.

Thank you for the comment. We agree to soften the claim of PT “attenuating” negative temporal changes in joint width and grip strength. The specific changes are listed as follows:

Abstract:

Line 26-27: PT-treated rats showed no significant time-dependent deterioration in joint width or grip strength over the 4-week period.

Results:

Line 93-94: The OA groups receiving AT and PT did not experience significant time-dependent changes in joint width

Line 98-99: Neither the normal control nor the OA groups receiving AT and PT showed significant time-dependent changes.

Discussion:

Line 208-213: In contrast, rats receiving PT maintained stable grip strength throughout the 4-week treatment period, with no significant temporal decline. However, since the post hoc com-parisons at week 4 did not reach statistical significance between the PT and OA control groups (unlike the GS group), PT should be interpreted as stabilising functional performance over time rather than actively enhancing joint strength under the present experimental conditions.

Please report and discuss the treatment × time interaction for the longitudinal outcomes. This is particularly relevant for grip strength because Table S1 reports a significant treatment × time interaction (p=0.0433), whereas the Results section focuses primarily on the separate treatment and time effects. The interaction is arguably the most informative statistic for determining whether the trajectories differed among treatment groups and should therefore be explicitly reported in Section 2.1 and, where appropriate, followed by clearly described post-hoc comparisons.

Thank you for the suggestion. We have added the time × time interaction effects for all results analysed using mixed-design ANOVA (Line 85-86, 90-91, 96-97).

There appears to be an inconsistency between the main text and Supplementary Table S1 regarding phosphorylated NF-κB. Section 2.4 states that no significant difference in phosphorylated NF-κB was detected across groups, whereas Table S1 reports a significant overall Kruskal–Wallis result for p-NFκB (H=14.67, p=0.0054), with the note that Dunn’s post-hoc comparisons did not identify significant pairwise differences. The Results should distinguish between a significant omnibus test and the absence of significant post-hoc pairwise comparisons rather than describing the parameter simply as showing “no significant difference.”

Thank you for the comment. We have added the following to the results in section 2.4.

Line 157-158: Kruskal-Wallis test revealed an omnibus significant difference in phosphorylated Nfkb (p=0.005), but not in total and the ratio of phosphorylated/total Nfkb among the groups (p>0.05).

The interpretation of the histological findings for PT should remain restricted to the structural component of the Mankin score. PT significantly reduced the structural score compared with the OA control, but did not significantly improve the cellular, matrix, tidemark, or total Mankin scores. Thus, wording such as “reduced cartilage structural damage” is appropriate, whereas broader statements implying overall histological protection should be avoided. This distinction is particularly important because GS, unlike PT, significantly improved the structural, cellular, and total scores.

Thank you for the comment. We agree with your insightful observation and make the following changes to restrict the PT-associated histological changes to the structural compartment.

Results:

Line 112-114: PT significantly reduced the structural score compared with the OA group (p=0.002), but did not alter the other components or the total Mankin score (p>0.05).

Discussion:

Line 219-220: GS showed the best performance in attenuating adverse joint changes, whereas PT only improved structural changes.

The authors should clarify the nomenclature of the Wnt target measured by qRT-PCR. The Methods and Results repeatedly refer to “Wnt” expression, while Table 2 identifies the primer specifically as Wnt3a. The manuscript and Figure 4 should consistently report Wnt3a if this is the transcript that was actually quantified. This is important because “Wnt” refers to a family of ligands rather than a single gene.

Thank you for the reminder. We have replaced the name “Wnt” with “Wnt3a” when the results of qRT-PCR were referred to.

The vehicle difference between PT and the remaining groups deserves slightly clearer treatment in the interpretation of the PT effect. PT was diluted in refined olive oil, whereas the normal control, OA control, AT, and GS groups received distilled-water-based preparations. The authors appropriately acknowledge this limitation, but because there was no olive-oil vehicle control, the observed PT effect cannot be unequivocally attributed to the tocotrienol-rich mixture alone. I suggest explicitly stating this point when interpreting the PT-versus-OA comparisons, rather than restricting it to the limitations paragraph.

Thank you for the insightful comment. We agree that the lack of a refined olive oil-supplemented OA control prevents us from attributing the effects of tocotrienol-rich mixture alone. Therefore, the following statements were added to alert the readers when interpreting the results.

Discussion:

Line 194-197: However, because PT was administered in a refined olive oil vehicle while the OA groups received distilled water, these initial trends must be interpreted with caution, as vehicle-related fatty acid contributions cannot be completely ruled out.

Line 240-243: However, it is important to note that without a dedicated olive-oil vehicle control group, the observed structural preservation associated with PT supplementation cannot be unequivocally attributed to the tocotrienol components, but rather to the PT–olive oil formulation as a whole.

Conclusion:

Line 493-495: As PT was delivered in refined olive oil, the potential confounding contribution of the vehicle should be taken into account when interpreting these outcomes.

The discussion of the AT findings should avoid implying structural worsening beyond what was directly demonstrated. The molecular findings for AT are interesting, particularly the increases in Il1b, Mmp13, Sost, and Ctnnb-related measures; nevertheless, the manuscript itself notes that clear evidence of structural worsening was not demonstrated. Moreover, the principal histological comparisons reported for AT are against the GS group rather than showing a significant worsening relative to the OA control. Statements such as “AT causes more severe damage” should therefore be revised to wording such as “AT was associated with a more catabolic molecular/transcriptional profile under the present experimental conditions.”

Thank you for the comment. We agree that the discussion of changes associated with AT supplementation should be more conservative. In line with that, the following statements were included:

Abstract:

Line 33-35: AT is associated with a catabolic transcriptional pattern. Nevertheless, AT did not cause explicit cartilage structural worsening or pathway activation under these conditions.

Discussion:

Line 221-223: In contrast, total Mankin scores in the AT-treated group were significantly higher than those in the GS-treated group, but not significantly different from those in the normal control group.

Conclusion:

Line 491-493: AT is associated with a more catabolic molecular profile, although clear evidence of signalling activation or structural worsening has not been demonstrated.

Please clarify the interpretation of serum COMP, particularly the OA+AT versus OA+GS difference. The only reported significant COMP comparison was a lower value in the AT group than in the GS group, while no other between-group differences were detected. The subsequent suggestion that lower COMP in AT-treated animals might indicate insufficient ECM synthesis is explicitly speculative and is not supported by additional synthesis/degradation biomarkers in this experiment. I recommend shortening this interpretation and making clear that the COMP data do not independently support a detrimental effect of AT.

Thank you for the comment. We agree that our original speculation was overextended and not substantiated by complementary cartilage turnover biomarkers. Hence, we have shortened the paragraph as follows:

Line 244-250: Circulating COMP is conventionally evaluated as a marker of cartilage matrix turnover. In the present study, the only statistically significant difference observed was lower serum COMP levels in the AT-treated group compared with the GS-treated group, with no significant differences detected relative to the untreated OA control or normal groups. Since serum COMP levels were not significantly elevated in AT-treated animals compared with controls, these data do not independently support a detrimental or catabolic effect of AT on cartilage matrix integrity under the present experimental conditions.

The authors should provide a little more methodological detail for the qRT-PCR quality-control procedure. The manuscript reports RNA concentration/optical purity and use of the 2^-ΔΔCt method with Gapdh, but does not indicate whether amplification specificity (e.g., melting-curve analysis), primer efficiency, and technical replicate measurements were assessed. Given that several central conclusions are based on relatively selective transcript-level changes (particularly Il1b, Mmp13, Sost, and Ctnnb), these details would improve reproducibility without requiring additional experiments.

Thank you for the comment to improve the clarity of qRT-PCR methodology. We have added the following:

Section 4.11

Line 439-440: Quantitative PCR amplification was conducted in technical duplicates for each sample.

Line 448-453: Following thermal cycling, melting-curve analysis was conducted according to the standard protocol in the MIC PCR Workbench (Bio Molecular Systems, Queensland, Australia). Samples were heated from 72°C to 95°C at a rate of 0.3°C/s. Raw fluorescence signal drops were converted by the software into derivative plots (-dF/dT vs. temperature) to verify single, distinct melting peaks for each target gene and rule out non-specific amplification or primer-dimer formation.

The final translational statement regarding PT as an adjunct or alternative intervention should be moderated. The present study is a four-week MIA rat experiment with n=6/group, and the authors themselves acknowledge that inflammatory changes may have subsided by the sampling point, that treatment/grip-strength assessment was unblinded, and that the AT dose has limited translational comparability. Accordingly, the statement that PT “may serve as a therapeutic adjunct or an alternative intervention for patients with OA who are unsuitable for conventional GS treatment” goes somewhat beyond the current evidence. It would be more appropriate to conclude that the findings support further preclinical evaluation of PT, including its potential combination with GS, before making a patient-oriented therapeutic positioning.

Thank you for the comment. We agree that, given the limitations in sample size, sampling frame, treatment period, and other potential biases in the methodology, the conclusion should be softened. The last statement on clinical translation has been replaced with the following:

Line 498-502: Therefore, these findings should not be interpreted as supporting immediate clinical replacement of conventional therapies. Instead, this study provides a rationale for further preclinical investigation of PT, including longer-term chronic OA models and combined regimens with GS, to fully characterise its potential prior to patient-oriented translational positioning.

Final remarks: Thank you again for your time in reviewing the manuscript. We hope the revised manuscript can meet the standards of the journals.

Reviewer 2 Report

Comments and Suggestions for Authors

In the study “Divergent Effects of Palm Tocotrienol-Rich Mixture and Alpha-Tocopherol on Joint Health in a Rat Model of Osteoarthritis Induced with Monosodium Iodoacetate” the authors compared the effects of a palm tocotrienol-rich mixture and alpha-tocopherol on joint protection in a rat model of induced osteoarthritis. While the manuscript presents interesting findings, the following points require clarification.

The abstract methods in lines 21 to 27 emphasize details such as types of rats, injection route, and dosage. While these are important, they are more appropriate for the Methods section in the main text. In the abstract, the methods should instead highlight what was done and how outcomes were measured.
Since the error bars of the normal group extend into the same range as OA (around score 1.0) in the Mankin structural score in Figure 3A, I don’t understand how the statistical test reports significance. Could you explain?
A total Mankin score of 2-3 in Figure 3E suggests mild damage/early-grade osteoarthritis; why didn't the authors use severe osteoarthritis in the study? Needs clarification.
Could you provide the blot that shows the entire band? It looks like the total Nfkb bands in Figure 5G are partially cut off.
The authors have mentioned that the palm tocotrienol‑rich mixture was diluted in refined olive oil, while alpha‑tocopherol was dissolved in water. However, refined olive oil alone vehicle control is not described in the manuscript. For better clarity and rigor, the authors should include this vehicle control group. This will help ensure that the observed effects are solely due to the tested agents rather than the solvents.
The authors have administered palm tocotrienol‑rich fraction at 100 mg/kg body weight in rats. However, a recent study published in Toxicology in Vitro (1016/j.tiv.2025.106062) reported that the tocotrienol-rich fraction from palm oil at concentrations above 1 mg/mL induced toxicity and morphological malformations in zebrafish embryos. Could the authors please provide a toxicological justification for the chosen dose (100 mg/kg) in rats, including reference to existing safety data? Please clarify whether the administered dose falls within established safe ranges.
For better clarity and strengthened transparency, the authors can present the limitations of the study in a separate paragraph under the heading “Limitations of the Study” if the guidelines of the journal permit.
Please enhance the visibility of the supplementary Western blot labels and clarify whether raw blot data are provided.

Author Response

Dear reviewer,

Reviewer 2

Title: Divergent Effects of Palm Tocotrienol-Rich Mixture and Alpha-Tocopherol on Joint Health in a Rat Model of Osteoarthritis Induced with Monosodium Iodoacetate

ID: pharmaceuticals-4548459

Comment

Thank you for your meticulous review. Your constructive comments have been carefully considered and replied as the following.

The abstract methods in lines 21 to 27 emphasize details such as types of rats, injection route, and dosage. While these are important, they are more appropriate for the Methods section in the main text. In the abstract, the methods should instead highlight what was done and how outcomes were measured.

Thank you for the comment. We have been instructed by the editor to keep the details of rats, injection route and dosage of treatment in the abstract. However, we have also considered the reviewer’s suggestion and added more description of the methods in the abstract. We have also condensed the abstract into 250 words.

Since the error bars of the normal group extend into the same range as OA (around score 1.0) in the Mankin structural score in Figure 3A, I don’t understand how the statistical test reports significance. Could you explain?

Thank you for the comment and for allowing us to explain the statistical interpretation in Figure 3A.

Unlike other measures in this study, Mankin scores are discrete ordinal measures analysed using Kruskal-Wallis test and displayed with box plots. The box plots display median and interquartile range (IQR) rather than mean ± standard error. Kruskal-Wallis test evaluates the shift in medians and rank distributions rather than overlapping extreme values (whiskers), the strong cluster of zero scores in the Normal and OA+PT groups compared to the consistent elevated scores in the OA group accounts for the reported statistical significance.

A total Mankin score of 2-3 in Figure 3E suggests mild damage/early-grade osteoarthritis; why didn't the authors use severe osteoarthritis in the study? Needs clarification.

Thank you for this insightful observation. The decision to use a mild/early OA model is aligned with the proposed use of palm tocotrienol-rich mixture as a preventive agent to delay OA progression. Once end-stage cartilage destruction is reached, regeneration would be limited. Therefore, mild/early-stage OA represents the optimal stage to intervene.

To address the reviewer’s concern, we have added the following in the limitations:

Line 299-303: In addition, MIA induction for 4 weeks yielded early-to-moderate structural alterations (as evidenced by a total Mankin’s score of 2–3), reflecting early-stage OA. Evaluating potential disease-modifying agents during early-grade OA is clinically relevant, as early intervention offers the best opportunity to preserve the remaining cartilage architecture before irreversible, end-stage structural failure occurs.

Could you provide the blot that shows the entire band? It looks like the total Nfkb bands in Figure 5G are partially cut off.

Thank you for the comment. We have replaced the total Nfkb bands in Figure 5G. All full blots are provided in the file for review.

The authors have mentioned that the palm tocotrienol‑rich mixture was diluted in refined olive oil, while alpha‑tocopherol was dissolved in water. However, refined olive oil alone vehicle control is not described in the manuscript. For better clarity and rigor, the authors should include this vehicle control group. This will help ensure that the observed effects are solely due to the tested agents rather than the solvents.

Thank you for the comment. We apologise for the oversight on our part in not including a refined olive oil control group. Since re-experimentation could not be performed at this juncture, we have included this limitation in the discussion.

Line 324-328: Refined olive oil was used as the vehicle for PT but it was not administered to the other groups. Refined olive oil is reported to contain less phytochemicals, but its fatty acid composition (for example, oleic acid) might still have health-enhancing effects, which temper the effects of PT. Thus, the effects of PT demonstrated in this study should be interpreted with caution because the solvent effects cannot be fully excluded.

The authors have administered palm tocotrienol‑rich fraction at 100 mg/kg body weight in rats. However, a recent study published in Toxicology in Vitro (1016/j.tiv.2025.106062) reported that the tocotrienol-rich fraction from palm oil at concentrations above 1 mg/mL induced toxicity and morphological malformations in zebrafish embryos. Could the authors please provide a toxicological justification for the chosen dose (100 mg/kg) in rats, including reference to existing safety data? Please clarify whether the administered dose falls within established safe ranges.

Thank you for the suggestion. We have added a paragraph to discuss the safety of palm tocotrienol-rich mixture as follows. Generally, these studies showed that the dose used (100 mg/kg/day) falls within the safety ranges reported in oral toxicity studies.

Line 272-283: Several studies have examined the toxicity aspect of PT. A study on Fischer 344 rats reported the no-observed-adverse-effect level for PT as 120 mg/kg bw/day for male rats and 130 mg/kg bw/day for female rats, based on changes in haematological and liver profile [41]. In another study, 28-day oral supplementation with PT up to 250 mg/kg in female BALB/c mice did not show significant adverse changes in the biochemical profile and liver histology [42]. This dose is equivalent to 107 mg/kg in rats based on body surface area conversion [43]. A recent study showed that exposure to PT below 500 μg/mL in zebrafish embryos caused no significant morphological changes [44,45]. Taken together, these pre-clinical safety thresholds consistently exceed or align with the 100 mg/kg bw/day dose administered in the current study. Therefore, the oral dose of PT utilised here falls well within the established safety margin for rodent models, ensuring that the observed joint-protective outcomes occurred in the absence of systemic toxicity.

For better clarity and strengthened transparency, the authors can present the limitations of the study in a separate paragraph under the heading “Limitations of the Study” if the guidelines of the journal permit.

Thank you for the suggestion. We have added the subheading as suggested.

Please enhance the visibility of the supplementary Western blot labels and clarify whether raw blot data are provided.

Thank you for the comment. We have enhanced the supplementary Western blot lables. The raw data have been included in the file for review.

Final remarks: Thank you again for your time in reviewing the manuscript. We hope the revised manuscript can meet the standards of the journals.

Reviewer 3 Report

Comments and Suggestions for Authors

This manuscript investigates the effects of a palm tocotrienol-rich mixture and alpha-tocopherol on osteoarthritis development. The authors compare the effects of PT and AT through joint function assessment, histological evaluation, and analysis of inflammatory, cartilage degradation, and signalling-related markers. The study is interesting and provides a relatively comprehensive experimental design to explore the different biological activities of PT and AT. The findings may provide useful information for understanding the potential application of vitamin E derivatives in joint health and osteoarthritis management.
I have the following review comments:

1. Each group contained only six animals. this sample size is too small for animal test.
2. The authors describe the model as representing early-stage OA, is the model sufficiently severe to evaluate disease-modifying effects? OA phenotype appears relatively mild, the protection effect may be not obviours.
3. The study includes GS as a positive control, the manuscript should better compare the PT/AT and GS, and discuss the potential of PT in replacing GS.
4. Regarding the analysis of Ctnnb and Nfkb were analyzed, the manuscript should clearly describe how phosphorylation ratios were calculated (e.g., phosphorylated protein/total protein normalization method).
5. data are presented as "mean ± SEM" in figures, presentation of individual data points would be more appropriate because mean ± SEM may underestimate biological variability.
6. grip strength is interpreted as joint function, but the inverted wire mesh test measures whole-body muscular endurance rather than joint-specific function. Therefore, using it as a direct measure of knee joint function maybe bias.
7. line 330: rephrease this sentence: "this study provides the first direct, head-to-head comparison evaluating the comparative efficacy of...", "comparison" and "comparative efficacy" express the same idea, it is redundant.

Author Response

Dear reviewer,

Thank you for reviewing our manuscript and provide the constructive comments. We have considered all comments and provided line-by-line replies in the attached response sheet. The changes in the text are highlighted in yellow. We hope the revised manuscript can meet the standards of the journal.

Thank you.

Author Response File: Author Response.docx

Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

The authors dissolved palm tocotrienol in olive oil but did not include an olive oil-alone vehicle control. Since olive oil is well known for its biological activity, including antioxidant, anti-inflammatory, neuroprotective, cardioprotective, and anti-cancer properties due to its bioactive components, omission of this olive oil-alone vehicle control is a major limitation. Without a proper vehicle control, it is unclear whether the observed effect is due to palm tocotrienol or olive oil or both, and the statistical significance becomes questionable.

The authors also acknowledge that “olive oil may have health-enhancing properties, and the observed effect could be partly due to the effects of PT demonstrated in this study should be interpreted with caution because the solvent effects cannot be fully excluded”.

Given that the title “Divergent Effects of Palm Tocotrienol-Rich Mixture and Alpha-Tocopherol on Joint Health in a Rat Model of Osteoarthritis Induced with Monosodium Iodoacetate” emphasizes the effects of palm tocotrienol in a rat model of Osteoarthritis, the data do not support this central claim. Hence, the study cannot be accepted in its current form unless the experiments are repeated with appropriate controls. Therefore, I must reject the manuscript at this time. The authors are encouraged to repeat the study with proper controls and resubmit.

Author Response

Dear reviewer,

Thank you.

Author Response File: Author Response.docx

Reviewer 3 Report

Comments and Suggestions for Authors

The authors have well addressed my questions.

Round 3

Reviewer 2 Report

Comments and Suggestions for Authors

Vehicle control is indispensable to ensure the observed effects are due to the tested compound and not the vehicle itself. Without proper vehicle control, the study can lead to inaccurate conclusions. While the authors acknowledge this as a limitation, the omission fundamentally undermines the study’s conclusions. The results rest on an assumption rather than experimental evidence; therefore, the manuscript cannot be accepted in its current form.