Dear Editor, The dismissal of small-sample intensive care unit (ICU) studies conflates sample size with methodological quality. As Ioannidis [1] famously argued, “most published research findings are false” in part due to biases that are not mitigated by increasing sample size alone. This concern is echoed in the broader methodological literature, where overreliance on p-values and power calculations has been widely criticized [2]. I argue that in critical care, sample size must be judged against the clinical, legal, and statistical context of the question asked. Sample size is a function of effect size, variance, and design assumptions, not an intrinsic marker of study quality.

Three constraints make large enrolment in the ICU structurally difficult, not merely inconvenient. First, the population of critically ill patients shows profound physiological heterogeneity, with trajectories that shift within hours. For rare syndromes or complex phenotypes, single-centre target populations may remain insufficient over years of recruitment, and multicentre designs are not always feasible. Second, the legal framework for consent creates asymmetric research conditions across jurisdictions. Incapacity to consent (e.g. from sedation, delirium, encephalopathy, or mechanical ventilation) is the rule, not the exception. In the United States, 21 CFR 50.24 permits Exception From Informed Consent (EFIC) for emergency research under community consultation and IRB oversight. The EU Clinical Trials Regulation (No 536/2014) allows enrolment without prior consent in emergencies, but implementation across member states is heterogeneous and procedurally complex, producing delays in time-critical conditions such as septic shock or cardiac arrest even where deferred consent is legally available. These disparities have direct, quantifiable effects on enrolment. Third, the statistics. In the two-proportion framework, required N is inversely proportional to the square of the effect size. With a control event rate of 40%, an absolute risk reduction (ARR) of 15–20% reaches adequate power with roughly 50–120 patients per arm. A 20% ARR in 28-day mortality corresponds to a number needed to treat of 5, consistent with the magnitude of established ICU interventions, such as prone positioning in severe ARDS (ARR ≈17% in PROSEVA [3]). For continuous outcomes, required N depends on the ratio of variance to the minimum clinically important difference. In ICU populations, where physiological variability is typically high, this ratio inflates sample-size requirements even when the intervention effect is substantial.

Small studies have repeatedly produced signals that shaped definitive trials. Amato et al. [4] (N = 53) first demonstrated a mortality reduction with a lung-protective strategy in acute respiratory distress syndrome (ARDS), later confirmed by the ARDSNet ARMA trial [5] (N = 861), which established ventilation at 6 mL kg^–1 predicted body weight as standard of care. The Rivers et al. [6] single-centre trial of early goal-directed therapy in septic shock (N = 263) transformed resuscitation practice for over a decade, though its mortality benefit was later relativized by ProCESS [7], ARISE [8], and ProMISe [9] showing that positive trials are hypothesis-generating, not verdict-delivering [10].

I propose that reviewers and editors replace numerical thresholds with a contextual appraisal:

The first three questions operationalise established reporting and evidence-grading principles (CONSORT 2025 [11]; GRADE [12]). The latter two, on jurisdictional consent reporting and feasibility, are not codified in current reporting standards but engage design challenges recognised by the critical care trialist community [13].

A study of 30–70 patients per arm can be adequate to detect the effect sizes that matter most in high-mortality ICU populations, provided the effect is real and the design is sound. The question, not the N, should be the primary criterion of scientific value.