Writing in Anesthesiology and Perioperative Science, researchers Xintong Zou, Suwen Hu and Yun Dong commend the original randomized controlled trial by Yao and colleagues as rigorous and valuable preliminary work, but they argue that several methodological and clinical issues must be resolved before the findings can be considered clinically meaningful rather than merely statistically significant.
The central concern raised in the letter concerns the size of the benefit. The original trial reported a reduction in Day 1 Numeric Rating Scale (NRS) pain scores that reached statistical significance, with a mean difference of −0.73 points and a P value of 0.001. The letter writers point out that a widely cited benchmark for the minimal clinically important difference (MCID) in acute pain, derived by Myles and colleagues using a 100-millimetre visual analog scale, is approximately 10 millimetres, roughly equivalent to one point on an 11-point NRS. Measured against that conservative benchmark, the observed difference of −0.73 falls below the threshold at which patients themselves would typically judge the change worthwhile.
The letter is careful to acknowledge the limits of this comparison. The conversion from the visual analog scale to the NRS is an approximation rather than a strict numerical equivalence, because the two scales differ in granularity and in how readily patients can discriminate between adjacent scores. Moreover, the authors stress that the MCID is not a fixed constant: it varies with the type of surgery, the baseline severity of pain, and the timing of assessment. They note that literature specific to head and neck endoscopic nasal surgery is lacking, and that extrapolating general surgical MCID values to this population may be inappropriate, underscoring the need for procedure-specific validation before firm conclusions are drawn.
Beyond the choice of benchmark, the letter argues that postoperative pain intensity after endoscopic nasal surgery may be shaped by a range of perioperative factors, and it calls on future trials to document and adjust for these variables systematically in order to minimize confounding. The writers also recommend complementing mean comparisons with a responder analysis, for example the proportion of patients achieving at least a 30 percent reduction in NRS score or reaching a patient acceptable symptom state, which they define as a visual analog score of 33 millimetres or less, approximately NRS 4 or below. Such analyses, they argue, better capture individual clinical benefit than group averages alone.
Supporting their skepticism about the size of the effect, the letter highlights the original trial’s finding on rescue medication: the proportion of patients requiring rescue non-steroidal anti-inflammatory drugs was 13.3 percent in one group versus 10.0 percent in the other, with a P value of 1.000. The letter writers describe this absence of a significant difference as consistent with the limited clinical impact suggested by the sub-MCID pain reduction, while cautioning that the result should be interpreted cautiously given the limited statistical power of the trial. They also propose a future sensitivity analysis restricted to patients with moderate-to-severe baseline pain, defined as NRS 4 or higher, to assess whether TEAS confers meaningful benefit in the subgroup most likely to respond.
A second major line of criticism concerns the statistical handling of secondary outcomes. The letter acknowledges that the original authors appropriately prioritized their primary outcome, but it notes that the numerous secondary hypothesis tests were conducted without prespecified hierarchical analysis or multiplicity adjustment, such as a Holm-Bonferroni procedure or false discovery rate control, which may elevate the family-wise error rate. At the same time, the writers concede that strict Bonferroni correction can be overly conservative when outcomes are clinically correlated, and that secondary outcomes are more appropriately interpreted as exploratory rather than confirmatory. This caveat applies particularly to the trial’s hemodynamic data, in which sporadic differences emerged only at isolated time points without a clear temporal pattern; the letter argues such findings should not be overinterpreted as evidence of a mechanistic effect.
Blinding is a third area of concern. Because the original design compared active stimulation at 5 to 10 milliamperes with a sham condition of 0 volts, the sensory distinction between groups may have introduced expectation biases, even though the formal blinding assessment showed no significant group difference, with a P value of 0.83. The letter suggests that future trials adopt a low-intensity perceptible sham control, for example 0.5 milliamperes, to better match the sensory profiles of active and sham stimulation. It further recommends incorporating patients’ perceived sensation ratings alongside a standard blinding questionnaire and the Blinding Index to quantitatively assess blinding integrity, and it proposes including a non-therapeutic acupoint control group to help differentiate acupoint-specific effects from non-specific placebo responses.
The letter also identifies an apparent inconsistency in the original trial’s Table 5, which reports odds ratios with 95 percent confidence intervals even though the analysis is described as multivariable linear regression. Odds ratios, the writers note, derive from logistic rather than linear regression, a discrepancy they say requires clarification. They further argue that the original article does not clearly distinguish among baseline prognostic factors, post-randomization process variables, and potential mediators or markers of surgical complexity. Variables such as intraoperative propofol and remifentanil consumption may lie on the causal pathway between TEAS and postoperative pain, whereas surgery duration, anesthesia duration and blood loss may instead reflect surgical complexity rather than true mediators. These heterogeneous variables, the letter argues, should not be interpreted collectively as independent risk factors.
On the modeling question, the letter suggests that because the regression objective should be to identify risk factors for postoperative pain rather than to explore intervention mechanisms, future studies should categorize variables a priori and, where appropriate, exclude potential mediators to avoid attenuating the true treatment effect, or alternatively employ causal mediation analysis to decompose TEAS’s total effect into direct and indirect components. The writers add that with a sample size of 60 and 5 to 6 predictors, the model may be susceptible to overfitting, and they recommend a more parsimonious model or sensitivity analyses excluding post-randomization variables to strengthen the findings.
Finally, the letter addresses the analgesic-sparing rationale for TEAS itself. One key motivation for the technique is mitigating opioid-related adverse effects, and while the trial demonstrated a statistically significant reduction in intraoperative remifentanil consumption, the letter writers emphasize that this represents intraoperative opioid reduction rather than postoperative opioid sparing, the latter being the more clinically relevant endpoint for multimodal analgesia strategies. Postoperative opioid sparing was not assessed in the original study, given that non-steroidal anti-inflammatory drugs were used for postoperative rescue analgesia. The letter also notes that the original authors reported only the proportions of patients receiving rescue NSAIDs, without providing the cumulative dosage administered, such as total milligrams or milligrams per kilogram within 24 to 72 hours, leaving unclear whether TEAS reduced the quantity of NSAID consumption among those requiring rescue medication. The writers therefore urge future studies to report cumulative analgesic dose alongside the proportion of users to better capture the clinical utility of TEAS. In their summary, Zou, Hu and Dong conclude that Yao and colleagues have provided valuable preliminary evidence supporting TEAS at the Xi and Yuan acupoints for postoperative analgesia, but that the concerns outlined, particularly regarding clinical significance, the exploratory nature of unadjusted secondary analyses, missing postoperative analgesic dosage data, and methodological issues in the regression model, should be addressed to strengthen the conclusions and improve future study designs.
Subject of Research: Methodological critique of a randomized controlled trial of transcutaneous electrical acupoint stimulation for postoperative pain after endoscopic nasal surgery
Article Title: Comment on: The efficacy of transcutaneous electricalstimulation of the Xi and Yuan acupoints on postoperative pain after endoscopic nasalsurgery: a randomized controlled trial
Article References: Zou, X., Hu, S., & Dong, Y. (2026). Comment on: The efficacy of transcutaneous electricalstimulation of the Xi and Yuan acupoints on postoperative pain after endoscopic nasalsurgery: a randomized controlled trial. Anesthesiology and Perioperative Science, 4(1), Article 44. https://doi.org/10.1007/s44254-026-00192-z
Image Credits: AI Generated
DOI: 10.1007/s44254-026-00192-z
Keywords: transcutaneous electrical acupoint stimulation, TEAS, postoperative pain, endoscopic nasal surgery, minimal clinically important difference, randomized controlled trial, numeric rating scale, multivariable regression, blinding, opioid sparing, rescue analgesia, multiplicity adjustment
News Source: Ophelia Keating. (October 29, 2026). Pain Score Gains From Acupoint Stimulation After Nasal Surgery May Fall Short of Clinical Significance, Letter Argues. Scienmag.
