Cluster-randomised trials in Indian development contexts (school-level curriculum trials, village-level health interventions, panchayat-level information campaigns) produce more underpowered studies than any other design we see. The cause is almost always the same. The intra-cluster correlation coefficient assumed at the power-calculation stage was wrong, usually too low, so the pre-registered sample size was smaller than the trial needed to detect an effect.
The intra-cluster correlation, or ICC, is the fraction of total outcome variance that lies between clusters. Two children in the same school share a teacher, a headmaster, a socio-economic catchment and the same buildings. Two women in the same self-help group share a facilitator, a village and a set of collective norms. Observations from one cluster therefore carry less independent information than a random-sample calculation assumes. The correction for this, called the design effect, grows with the ICC and with cluster size.
The formula is standard. The trouble lies in where the ICC that goes into it comes from. In our review of pre-registered cluster RCTs in Indian education, health and livelihoods programmes over the last several years, the most common source was another paper. Sometimes that paper studied a similar outcome. Often it studied the same outcome in a different country, with a different sampling frame, at a different stage of programme implementation. Sometimes its own ICC came from a small pilot with a wide confidence interval. Copied often enough, such a number becomes a convention, and then the default that people plug in.
The ICCs observed in Indian development outcomes are higher than these conventions assume. For foundational literacy and numeracy indicators measured at the school level, they cluster between 0.10 and 0.25, while some published power calculations use 0.02-0.05. For infant and child anthropometrics at the village level, they run between 0.05 and 0.15. Self-reported behavioural outcomes such as contraceptive use, hand-washing practice and latrine ownership are often higher still, in the 0.15-0.30 range, because they reflect community norms as much as individual choice.
An ICC that is too low has a direct cost. Take a trial designed with ICC = 0.02, cluster size = 20 and 30 clusters per arm. It is powered to detect a certain minimum detectable effect on a certain outcome. If the underlying ICC is 0.10, the same trial can only detect an effect substantially larger than the MDE named in the pre-registration. When the true effect falls between the pre-specified MDE and that larger one, the trial will fail to reject the null and the programme will be reported as ineffective. The programme may have worked. The study could not have detected the effect it produced.
We recommend three practices, listed in ascending order of cost and of value.
First, take ICC estimates from the actual data source or a comparable one. The ASER micro-data allows village- and district-level ICC estimation for foundational literacy and numeracy in India. DHS-5 / NFHS-5 supports village-cluster ICC estimation for a wide range of health outcomes, and UDISE+ carries school-level administrative outcomes. Use data close to your setting, and check any ICC taken from a published paper before relying on it.
Second, show how the required sample changes with the ICC. Report the sample size needed for the target power at ICC = 0.05, 0.10, 0.15 and 0.25 for each outcome of interest. Those four numbers tell the funder and the reader of the pre-registration what the trial is committing to. A single-point estimate hides that model uncertainty, and the sensitivity table puts it in view.
Third, budget for a real baseline. A pilot survey of five to eight clusters early in the trial timeline gives an in-sample ICC for the actual outcome variable at the actual measurement frequency, and it is the only way to know whether the assumed ICC is close. In our experience, an ICC estimated from a pilot in the sampled population differs meaningfully from one taken from external sources about seventy per cent of the time. The pilot costs little next to the trial. Skipping it moves the risk to the endline.
A further point concerns cluster size and the number of clusters. On a fixed budget, adding one cluster raises power far more than adding one observation inside an existing cluster. This follows directly from the design effect, and field practice often overlooks it. When budget conversations settle on "more surveys per village to reduce cost per interview," the resulting design is usually less powerful than one that spends the same money on fewer surveys in more villages. The right trade-off depends on the ICC, which is a second reason to estimate it.
Pre-registration standards require the ICC assumption to be reported, but journal reviewers rarely check it against the range observed for that outcome. A trial that reports ICC = 0.02 for a foundational-literacy outcome at the school level in India is asking the reader to accept a value an order of magnitude below the plausible range. Occasionally that value is right. Usually it is a convention that has drifted away from what the data show.
Useful references: Hemming and Marsh's tutorial on sample size for cluster-randomised trials; Hedges and Hedberg's paper on intraclass correlation values for education outcomes; and the J-PAL power calculation resource for practical templates.