Abstract
We read with interest the recent systematic review and meta-analysis by Kim et al on acupuncture and moxibustion for non-small cell lung cancer (NSCLC). 1 While the review addresses a clinically relevant supportive-care question, several methodological issues may lead readers to overestimate certainty.
First, the clinical question is not as focused as the title and conclusion suggest. The review pooled trials across perioperative and chemotherapy settings, and across markedly different problems including postoperative cough, pain, cancer-related fatigue, and chemotherapy-induced nausea and vomiting. It also mixed usual supportive care, chemotherapy-based regimens, analgesic-based regimens, sham-TEAS controls, and even an untreated comparator. Such clinical diversity is not incidental background noise; it changes the estimand. The pooled effect may therefore reflect a broad bundle of supportive-care contexts rather than a coherent estimate for “NSCLC patients undergoing standard treatment.” This also weakens the claim of novelty, because a prior NSCLC-specific synthesis had already evaluated acupuncture or moxibustion alongside chemotherapy, albeit with different outcomes. 2
Second, the eligibility criteria were not applied consistently. The Methods defined the intervention as acupuncture or moxibustion added to standard care and comparators as standard treatment alone or sham-TEAS. Yet Table 1 includes pharmacopuncture, topical herbal application, acupoint patching, acupuncture plus codeine, acupuncture plus ubenimex, and a moxibustion-versus-untreated trial. These co-interventions and non-equivalent controls make attribution of effect to acupuncture or moxibustion alone difficult and substantially increase indirectness.
Third, outcome selection appears to have drifted materially from the registered protocol. The authors acknowledge that the original PROSPERO record focused on RECIST and survival, whereas the final review selected quality of life, chemotherapy-induced nausea and vomiting, and immune markers, and screened studies according to whether they reported at least one of those outcomes. 1 For a derivative review, this may be defensible, but PRISMA 2020 still expects transparent reporting of outcome changes and analytic decisions. 3 In practice, selecting studies after seeing which outcomes were reported can introduce selection bias at the review level and should have been handled as a formal protocol amendment, not only as a retrospective explanation.
Fourth, the risk-of-bias assessment seems overly permissive. The article uses a modified seven-item approach rather than a domain-based contemporary framework, and some judgments are difficult to justify. Merely stating that randomization occurred does not establish low risk; lack of a published protocol does not automatically make selective reporting “unclear” for all trials; and unequal group sizes or dropouts do not by themselves determine attrition bias. More importantly, most included trials were open-label and evaluated highly subjective outcomes such as QLQ-C30 and KPS, while only two sham-controlled studies were included. Under RoB 2, deviations from intended intervention and outcome measurement would likely warrant more caution.4,5
Finally, several internal inconsistencies further reduce confidence in the pooled estimates. The manuscript reports nine databases in the abstract but ten in the Methods, while the PRISMA figure lists databases and automation-related exclusions not clearly described elsewhere. Binary KPS improvement is reported with an effect labeled as mean difference rather than risk ratio. For TNF-α, the reported confidence interval excludes the null comfortably, yet the text gives P = .04, which is discordant with the forest plot. The authors also excluded one global health status study because its negative mean difference was “likely” due to an alternative interpretation of scoring. Such post hoc exclusion is especially concerning when heterogeneity remained high after the exclusion.
We believe this review remains clinically interesting, but its conclusions should be framed more cautiously. A more defensible interpretation is that low-certainty evidence suggests possible benefit for some supportive-care symptoms, whereas the magnitude and specificity of effect for acupuncture or moxibustion in NSCLC remain uncertain until future reviews use a narrower clinical question, protocol-concordant eligibility criteria, sham-sensitive subgrouping, and contemporary bias assessment.
