We sincerely appreciate the interest in our recently published article entitled “Efficacy and safety of low-dose naltrexone for the management of fibromyalgia: a systematic review and meta-analysis of randomized controlled trials with trial sequential analysis,” in the Korean Journal of Pain [1]. We would like to thank Dr. Due Bruun and colleagues for their careful review and constructive feedback [2], and we appreciate the opportunity to respond to their thoughtful comments and clarify the points raised in this correspondence.

We appreciate the opportunity to clarify the issue regarding the outcome of “at least 30% improvement in pain symptoms.” We acknowledge an oversight in data extraction from the study by Due Bruun et al. [3]. The error arose because the extraction was based solely on the information presented in Table 2, which reported “30% improvement in pain.” This was initially interpreted as referring exclusively to participants who achieved a 30% improvement, without including those who experienced a 50% improvement. Upon careful re-examination, and as correctly noted in the letter, the text of the original article indicates that the data presented under “30% improvement in pain” in Table 2 actually encompassed participants who achieved at least 30% improvement—including those with 50% improvement [3]. We sincerely regret this oversight in data interpretation. Nevertheless, this minor correction does not alter the overall conclusions of our meta-analysis, as low-dose naltrexone remains associated with a significantly greater proportion of patients achieving ≥ 30% improvement in pain compared with placebo among individuals with fibromyalgia, consistent with the findings highlighted in the correspondence.

We also appreciate the concern raised regarding the potential overestimation of the “Changes in Pain Scores” outcome. The letter suggested that standardized mean difference (SMD) should have been used to pool the effect estimates due to presumed differences in the reporting scales. However, we respectfully disagree with this interpretation. Among the four studies included, only one (Bested et al. [4]) clearly used a different pain measurement scale. The study by Paula et al. [5] utilized a Visual Analog Scale (VAS) with a 0–10 range, while the study by Due Bruun et al. [3] employed a Numeric Rating Scale (NRS) that, despite a different name, was likewise based on a 0–10 metric—thus comparable to the VAS. The study by Younger et al. [6] used a VAS ranging from 0–100, which was standardized to a 0–10 scale prior to analysis (e.g., a score of 11 was converted to 1.1). Therefore, three of the four studies ultimately reported pain intensity on a uniform or directly convertible scale. In accordance with methodological guidance, we prespecified the mean difference (MD) as the primary effect measure, as it preserves the natural units of the outcome and provides greater clinical interpretability while avoiding the limitations of unitless SMD estimates [7–9]. Moreover, as noted in the letter, the analysis using the SMD yielded considerably greater between-study heterogeneity (I² ≈ 94.9%) compared with the MD analysis (I² ≈ 33%). This marked discrepancy likely reflects the inherent dependence of SMD on within-study standard deviations (SDs), as SMD is calculated by dividing the mean difference by the pooled SD [8,9]. Consequently, SMD values are more sensitive to random variation in SD estimates, particularly in smaller studies where SDs tend to be less stable [8,9]. Such variability can artificially inflate between-study heterogeneity (I²), even when the absolute effects across studies are comparable [8,9]. In contrast, MD is independent of within-study SDs and therefore provides a more stable and interpretable pooled estimate when outcomes are measured using the same or directly comparable scales [9]. For these reasons, MD offers greater robustness and clinical interpretability in the present analysis [9].

The letter also raised concerns regarding the handling of data from several included studies, which we appreciate and would like to clarify. First, for the study by Bested et al. [4], we extracted data from period 2 rather than period 1 because, as stated in the Methods section of our original article, all data used for the meta-analysis were derived from the final follow-up period. Moreover, a washout period of 14 ± 2 days was implemented prior to period 2 to minimize potential carryover effects. Second, with respect to the study by Younger et al. [6], we respectfully disagree with the assertion that percentage data from the VAS cannot yield SD values. SDs were explicitly reported in the original publication, and numerous previous meta-analyses have validly utilized percentage-based data [10,11]. Change from baseline and percentage change from baseline may be analyzed as continuous outcomes in the same way as final value outcomes, as outlined in the Cochrane Handbook for Systematic Reviews of Interventions [7]. These percentage values still correspond to scores on a 0–100 VAS scale, which was converted to a 0–10 scale to ensure consistency across studies. Finally, for the study by Paula et al. [5], we included only data from the low-dose naltrexone (LDN) + sham transcranial direct current stimulation (tDCS) and placebo + sham tDCS groups. This decision was based on methodological rigor, as sham stimulation functions as a placebo control and does not introduce an active therapeutic effect. Including data from active tDCS arms could confound the outcomes by incorporating the analgesic effects of tDCS, thereby obscuring the true effects attributable to LDN or placebo alone.

We hope that the clarifications provided above adequately address the concerns and questions raised regarding our article.