Methodological Concerns Regarding the Partially Randomized Design and Statistical Inference in Preoperative TEAS for Breast Cancer Patients: A Letter to the Editor [Letter]

Dear editor

We read with great interest the article by Ma et al entitled “Preoperative Transcutaneous Electrical Acupoint Stimulation Alleviates Postoperative Pain and Improves Sleep Quality in Breast Cancer Patients with Preoperative Sleep Disturbance: A Partially Randomized Controlled Trial”, recently published in the Journal of Pain Research.¹ The authors should be commended for addressing an important clinical question—whether TEAS can benefit breast cancer patients with preoperative sleep disturbance—and for providing preliminary evidence that TEAS may reduce postoperative pain and improve sleep quality. However, several methodological concerns regarding the study design, statistical analysis, and clinical interpretation warrant careful consideration before these findings can be translated into clinical practice.

First, the partially randomized design introduces fundamental challenges for causal inference. Patients with PSQI < 6 were assigned to the non-randomized control group (Group C), whereas patients with PSQI ≥ 6 were randomly allocated to Group S (sleep disturbance) or Group T (TEAS). As the authors acknowledge, comparisons involving Group C versus Groups S or T are observational and should be interpreted as stratified by baseline sleep status rather than as randomized contrasts. Despite this important limitation, the authors repeatedly make claims that imply causal equivalence. In the Results section, they state that “pain scores in Group T were comparable to those in Group C across all time points, suggesting that preoperative TEAS effectively normalized postoperative pain perception”. However, this comparison is between a randomized intervention group and a non-randomized reference group with fundamentally different baseline characteristics—Group C had significantly lower preoperative PSQI (4.46 ± 0.76 vs 8.71 ± 1.36), lower AIS (3.92 ± 1.74 vs 7.82 ± 1.78), and lower SAS anxiety scores (29.23 ± 3.18 vs 31.99 ± 3.18). The observed “comparability” between Group T and Group C may merely reflect baseline differences rather than a genuine treatment effect. Regression to the mean—whereby patients with extreme baseline values tend to show greater improvement regardless of treatment—cannot be excluded. To strengthen causal attribution, the authors should limit their primary conclusions to the randomized comparison between Group S and Group T, and reframe any comparisons involving Group C as hypothesis-generating rather than confirmatory.²

Second, the absence of adjustment for surgical procedure type in regression analyses represents a major confounding concern. The authors performed linear regression analyses to examine associations between preoperative PSQI scores and postoperative outcomes (Figures 5–7), but these analyses were unadjusted for any covariates. Notably, Table 1 shows that modified radical mastectomy (MRM)—the most extensive and painful procedure—was performed in 42.3% of Group C, 31.3% of Group S, and 31.3% of Group T. As anesthesiologists and pain physicians, we recognize that surgical trauma is the single strongest determinant of acute postoperative pain intensity. An MRM patient with a PSQI score of 8 might experience NRS pain of 7, whereas a breast-conserving surgery patient with the same PSQI score might experience NRS pain of 4—yet the authors’ unadjusted regression would attribute both pain levels to PSQI alone. The authors should have performed multivariable regression or ANCOVA adjusting for at least surgical procedure type, baseline anxiety, and intraoperative opioid consumption to determine whether PSQI remains an independent predictor.³

Third, the absence of a sham-TEAS control group limits the ability to exclude placebo effects. The authors appropriately acknowledge this limitation in their discussion. However, this is not merely a minor methodological nuance—it fundamentally affects the interpretation of all subjective outcomes (NRS pain and AIS sleep scores). A meta-analysis of acupuncture versus sham acupuncture demonstrated that sham acupuncture has a considerable therapeutic effect.⁴ Moreover, the Acupuncture Trialists’ Collaboration’s updated individual patient data meta-analysis, including 39 trials and 20,827 patients, showed that approximately 60% of the effect of acupuncture is ascribed to nonspecific context effects plus sham, and only 40% to the specific benefit of true acupuncture.⁵ In the absence of a sham comparator, the observed differences between Group T and Group S could reflect a combination of true physiological effects, non-specific effects, and regression to the mean. We encourage the authors to frame their findings as preliminary evidence requiring confirmation in a sham-controlled, fully randomized trial.

Fourth, the designation of NRS as a co-primary outcome without formal sample size calculation warrants methodological scrutiny. The authors state that “postoperative NRS pain intensity was designated as a co-primary outcome of equal clinical importance; however, formal power calculation for NRS was not performed”, and rely on “post-hoc inspection” to justify the sample size. This approach violates fundamental principles of clinical trial design. When a study has multiple primary outcomes, appropriate adjustments for multiplicity should be applied to control the family-wise type I error rate.⁶ The absence of a priori power calculation for a co-primary outcome means the study may be underpowered to detect clinically meaningful differences in NRS, and the post-hoc justification introduces substantial risk of false-positive findings. The authors should consider reclassifying NRS as a secondary or exploratory outcome.

In summary, Ma et al have conducted a clinically relevant investigation into the potential benefits of TEAS in breast cancer patients with preoperative sleep disturbance However, the partially randomized design, unadjusted regression analyses, lack of sham control, and issues surrounding co-primary endpoint designation substantially limit the strength of the conclusions. We respectfully suggest that the authors: (1) restrict confirmatory conclusions to the randomized comparison between Group S and Group T; (2) perform multivariable regression analyses adjusting for surgical procedure type, baseline anxiety, and intraoperative opioid use; (3) reframe their findings as preliminary and hypothesis-generating; and (4) reclassify NRS as a secondary outcome. Addressing these methodological concerns in future studies would substantially strengthen the evidence base for TEAS in perioperative care.

Disclosure

The authors report no conflicts of interest in this communication.