Modulation of Mu-Opioid Receptor Expression and Functional Impairment of Natural Killer Cells in Neuropathic Pain: Implications for Biomarker Discovery and Personalized Therapies

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

To improve the manuscript, the following changes should be included in the final version:

1. The introduction should include specific information on the incidence and/or prevalence of central neuropathic pain and peripheral neuropathic pain.
2. Currently, what are the main biomarkers for neuropathic pain? Include this relevant information in the manuscript's introduction.
3. It is necessary to indicate the intracellular pathways that are activated or suppressed in NK cells in relation to opioid receptors. This information should be included in the manuscript's introduction.
4. The authors should better explain the relationship between NK cells and the development of peripheral neuropathic pain. This information should be included in the manuscript's introduction.
5. The authors should highlight the novelty of the research and the potential clinical translation of the results. Include this information in the introduction of the manuscript.
6. In the results section (2.1), the authors state that "In mice, the CCI of the sciatic nerve causes debilitating symptoms, such as spontaneous pain, allodynia, hyperalgesia, and dysesthesia/paresthesia." How did they assess dysesthesia/paresthesia in mice with CCI lesions? What technique did they use? What results did they obtain regarding dysesthesia/paresthesia? Please clarify all these points and include this relevant information in the final version of the manuscript.
7. I believe Figure 1B is incorrect. Animals with neuropathic pain (CCI) typically withdraw their hind legs sooner in response to painful thermal stimuli, and therefore have a shorter withdrawal latency, compared to control animals. The figure in the manuscript is confusing. Please review the results and clarify this point in the final version of the manuscript.
8. The authors present the results obtained from the analysis performed on the NK cells. However, they do not establish any relationship between these changes in the NK cells and the levels of thermal hyperalgesia and mechanical allodynia. Please include figures showing the main changes in the NK cells in relation to the pain parameters. Include all this information in the final version of the manuscript.
9. In confocal microscopy figures, the calibration bar value must be included in the figure legend.
10. In the first sentence of the discussion, the authors should provide concrete data. How many millions of people worldwide suffer from peripheral neuropathic pain, which is the pain studied? What is the economic cost to these patients with peripheral neuropathic pain? Furthermore, it is also relevant to know how many of these patients have undergone similar studies on NK cell populations and opioid receptors. What clinical implications do the results obtained in this study have? Please include all this relevant information in the final version of the manuscript.
11. In the discussion, the authors should provide more specific data on clinical studies where similar assessments to those performed in the preclinical study have been carried out.
12. The discussion should include more detailed information on the mechanism by which opioid receptors influence NK cell physiology, and how this contributes to the development of peripheral neuropathic pain. This point needs further exploration in the discussion section.
13. The relevance of studying opioid receptors in NK cells as a potential mechanism for regulating peripheral neuropathic pain also needs to be discussed in greater depth.
14. The discussion should also delve deeper into the content of NK cells, which, when released, can induce peripheral neuropathic pain. These chemical mediators released by NK cells act on specific cellular elements (neurons, glial cells, or other cells), triggering peripheral neuropathic pain. Include all this information in the final version of the manuscript.
15. In the context of peripheral neuropathic pain, can it be said that NK cells are in an exhausted state? This point is very interesting and should be discussed in more detail. The authors could add more relevant information on this in the last paragraph of the discussion, before the limitations section.
16. Regarding the limitations and future directions section, while the identification of biological markers is indeed key for any pathology, the study does not establish a direct relationship between changes in NK cells, opioid receptor levels, and the degree of thermal hyperalgesia and mechanical allodynia. If such a relationship or correlation truly exists, the authors should demonstrate and discuss it.
17. What new therapies targeting opioid receptors in NK cells could potentially alleviate neuropathic pain if the relationship between these variables were indeed demonstrated? Include this information in the final version of the manuscript.
18. Why did the authors use only male mice in the study? Why didn't they include female mice? Please clarify this point and include this relevant information in the final version of the manuscript.
19. Why did the authors use ketamine to anesthetize the animals, given that this drug is known to significantly influence glutamatergic neurotransmission in the central nervous system? This could affect glutamatergic neurotransmission of nociceptive afferent fibers in the dorsal horn of the spinal cord. Please clarify these points and include this information in the final version of the manuscript.

Author Response

Please find the attached file

Author Response File: Author Response.docx

Reviewer 2 Report

Comments and Suggestions for Authors

The manuscript addresses the timely issue of identifying objective biomarkers for chronic neuropathic pain. The authors investigate µ‑opioid receptor (MOR) expression, degranulation (CD107a assay), granzyme A release, and IFN‑γ production in splenic NK cells from mice subjected to chronic constriction injury (CCI) of the sciatic nerve. The study is methodologically sound in several aspects, but concerns regarding experimental design and the robustness of conclusions limit the current version.

As main comments I would like to note the following:

1. The authors demonstrate correlations between CCI and NK‑cell changes (reduced surface MOR, impaired degranulation, decreased IFN‑γ). However, the design lacks any intervention (e.g., a MOR antagonist, adoptive transfer of NK cells, or pharmacological modulation). The observed NK‑cell alterations could be secondary to systemic inflammation, surgical stress, or other factors rather than a direct consequence of neuropathic pain. Without an interventional arm, it is difficult to claim that neuropathic pain causesthese changes, or that MOR on NK cells is a specific biomarker for neuropathic pain versus chronic stress or general inflammation. Acknowledge this limitation explicitly in the Discussion. For future work, propose experiments using naloxone (MOR antagonist) or adoptive transfer of NK cells from CCI mice to naïve recipients.
2. Even the sham procedure (nerve exposure without ligation) induces local inflammation and stress. The study only includes a sham control. An additional control group with a non-neural inflammatory model(e.g., subcutaneous carrageenan) or a stress‑only control(handling and behavioural tests without surgery) would be desirable. Some of the observed changes (MOR reduction, impaired CD107a expression, lower IFN-γ production) might reflect a non-specific surgical stress response rather than a pain-specific phenomenon. Discuss this possibility and avoid overstating the specificity of the findings.
3. All analyses are performed on splenocytes. Neuropathic pain might also alter NK cells locally - at the nerve injury site, in dorsal root ganglia, in the spinal cord, or in blood perfusing the injured area. It is unclear whether the splenic changes reflect a systemic phenomenon that is relevant to local pain mechanisms or simply a general immune shift. The authors should acknowledge that the link between splenic NK-cell alterations and central/peripheral sensitisation remains hypothetical. Ideally, blood or ipsilateral ganglia should be examined.

Some of the conclusions drawn by the authors appear premature.

Main conclusion: “MOR downregulation as a novel immunological hallmark / biomarker” Tentatively supported, but requires caution. What is proven: reduced surface MOR expression and receptor internalisation (confocal microscopy) in CCI mice compared to sham. What is NOT proven: specificity for pain (vs. surgery/inflammation/immobilization), correlation with pain intensity at the individual animal level (no regression or correlation analysis between %MOR+ NK cells and PWT or withdrawal latency provided), translational validity in humans (mouse model is only the first step). The statement “supporting its potential as a biomarker” is acceptable, but calling it a “novel immunological hallmark” is premature without cross-validation in another model or correlation with behavioural parameters at the individual level.

Conclusion of an “exhausted phenotype” in NK cells partially supported. It was shown reduced CD107a expression under unstimulated conditions (both total NK and Ly49C/I+ subset) and decreased IFN γ production after PMA/ionomycin stimulation. Concerns evidence: classic exhaustion markers (PD 1, TIM 3, LAG 3, TIGIT) were not measured. In immunology, “exhaustion” is a specific term for chronic antigen stimulation (cancer, chronic viral infection). This is a different context. Reduced functionality could also be due to anergy or suppression (e.g., by MDSCs or Tregs), not necessarily true exhaustion. PMA/ionomycin bypasses receptor signalling – a reduced response to such a strong stimulus does indicate a deep defect, but it could also reflect metabolic stress or general toxicity in CCI mice. Replace “exhaustion” with “functional impairment” or “hyporesponsiveness” unless exhaustion markers are provided.

Causal link between MOR downregulation and impaired degranulation / cytotoxicity. The authors show that MOR surface expression is reduced and the receptor is internalized, degranulation (CD107a) is reduced, granzyme A is detected extracellularly. However, no direct causal link is established. There is no experiment where: a MOR agonist restores (or worsens) degranulation or a MOR antagonist mimics the effects of CCI. In the Conclusions, the phrase “linking receptor modulation to decreased cytotoxicity” is an interpretation, not a proven fact.

The abstract states “increased frequency of inhibitory Ly49C/I expressing NK cells, pointing to altered NK cell education”. This point is not elaborated in the main text. No quantitative data on the activating/inhibitory receptor ratio are provided, and no functional blocking experiments for Ly49C/I are performed. The conclusion about “altered NK cell education” is speculative. NK cell education requires analysis of receptor repertoire in the bone marrow and cross tolerance studies. Either remove this statement or add supporting experiments (e.g., blocking antibodies).

Minor Comments and Corrections

1. Positive control for degranulation – PMA/ionomycin stimulation is relegated to Supplementary Figures 2 and 3. The main Results section (pages 7–8) only describes unstimulated conditions. At least a brief quantitative description of the stimulated condition should appear in the main text.
2. Granzyme A is not strictly specific for NK degranulation; it can also be released during necrosis or incomplete lysosomal fusion. The confocal images (Figure 7) show extracellular staining but without quantitative analysis.
3. MOR mRNA levels not examined. Internalisation does not rule out transcriptional downregulation. qPCR would clarify this. Without it, “reduction in surface expression” is correct, but “downregulation” implies a regulatory change at the mRNA or protein synthesis level – that should be demonstrated or softened.

After these revisions, the manuscript would become much more balanced and could be considered for publication.

Comments on the Quality of English Language

The English language is generally understandable and meets academic standards, but it contains a noticeable number of stylistic awkwardnesses, somewhat unnatural constructions ("non-native phrasing"), as well as several grammatical errors and typos. The manuscript requires language polishing before publication, particularly in the Results section and the figure legends.

I recommend a language editing before publication, preferably by a native English speaker or a professional editor. The main issues include articles, word order, duplicated text in the figure legends, and inconsistency in the designation of time points.

I did not find critical errors that change the meaning. The manuscript can be accepted after stylistic revision.

Author Response

Please find the attached file

Author Response File: Author Response.docx

Reviewer 3 Report

Comments and Suggestions for Authors

This is a strong mechanistic immunology-neuroscience study investigating the interaction between neuropathic pain and NK cell function, particularly focusing on μ-opioid receptor (MOR) modulation. The work is technically solid, biologically relevant, and clinically interesting, especially in the emerging field of immune-based pain biomarkers.However, there are key conceptual clarifications, methodological details, and translational gaps that need strengthening before publication in a high-impact journal.

Major Questions

1. The study demonstrates reduced μ-opioid receptor (MOR) expression and NK cell dysfunction in CCI mice, but how do the authors establish a direct causal relationship between MOR downregulation and NK cell functional impairment rather than a parallel inflammatory consequence of nerve injury?
2. The manuscript uses the term “NK cell exhaustion,” but the data do not include classical exhaustion markers such as PD-1, TIM-3, or NKG2A balance; how do the authors justify this conclusion without a complete exhaustion phenotype panel?
3. What experimental evidence supports that MOR internalization observed in NK cells is specifically triggered by neuropathic pain mechanisms rather than general stress or systemic inflammatory responses induced by surgery?
4. The study lacks pharmacological or genetic manipulation of MOR; how do the authors confirm that MOR signaling is functionally responsible for the observed NK cell alterations?
5. How was the specificity and validation of the anti-MOR antibody confirmed in NK cells, given the known controversy surrounding MOR detection in immune cell populations?
6. The study reports decreased CD107a expression and altered IFN-γ production, but how do the authors demonstrate that these functional changes are directly linked to MOR modulation rather than independent immune suppression?
7. Why were no human samples included to validate whether MOR downregulation on NK cells also occurs in patients with neuropathic pain, limiting translational relevance?
8. The sample size (n=6 per group) appears limited for multi-parametric immunological and behavioral analysis; how did the authors ensure sufficient statistical power and reproducibility?
9. Confocal microscopy images show MOR internalization, but why were quantitative colocalization analyses (e.g., Pearson’s coefficient) not performed to support these observations objectively?
10. Did the authors evaluate whether other immune cell populations (T cells, macrophages, B cells) show similar MOR modulation, or is this effect specific to NK cells?
11. How do the authors differentiate MOR downregulation as a specific biomarker of neuropathic pain versus a general marker of chronic inflammation or stress response?

Minor Questions

1. Several abbreviations are repeated or excessively listed; can the authors streamline the abbreviation section for clarity?
2. Were all flow cytometry and imaging analyses performed in a fully blinded manner, and if so, how was blinding ensured during data acquisition and analysis?
3. The manuscript states “NK cell exhaustion,” but would the authors consider revising terminology to “functional impairment” for greater scientific accuracy?
4. Some figure legends lack detailed quantification (e.g., exact gating strategy explanation in main text); can the authors clarify this for reproducibility?
5. Was any inter-assay or intra-assay variability assessed for CD107a, IFN-γ, and MOR measurements to ensure technical robustness?

Author Response

Please find the attached file

Author Response File: Author Response.docx

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The authors have made an effort to include the suggestions made by the reviewer.

Reviewer 2 Report

Comments and Suggestions for Authors

The authors have responded to all questions and addressed all comments. The manuscript can be published in its current form.

Reviewer 3 Report

Comments and Suggestions for Authors

I am satisfied with authors reply and would like to accept this manuscript.