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 reason is almost always the same. The intra-cluster correlation coefficient assumed at the power-calculation stage was wrong, usually low, and the pre-registered sample size did not reflect what the trial would actually take to detect an effect.
The intra-cluster correlation, or ICC, measures the fraction of total outcome variance that lies between clusters rather than within them. It is the reason clusters are not free. Two children in the same school share a teacher, a headmaster, a socio-economic catchment, and an infrastructure envelope. Two women in the same self-help group share a facilitator, a village context, and a set of collective norms. Observations from the same cluster carry less independent information than a random-sample calculation assumes, and the correction factor — the design effect — scales with the ICC and the cluster size.
The formula is not the interesting part. The interesting part is where the number that goes into the formula 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 way an ICC is chosen is by copying it from another paper. Sometimes the paper is on a similar outcome. Often it is on the same outcome but in a different country, from a different sampling frame, at a different stage of programme implementation. Sometimes the ICC is copied from a paper whose own ICC was derived from a small pilot with a wide confidence interval. The number becomes a convention. The convention becomes a plug-in default.
The empirical distribution of ICCs in Indian development outcomes is not what the conventions assume. In education outcomes measured at the school level, ICCs on foundational literacy and numeracy indicators cluster between 0.10 and 0.25, not the 0.02-0.05 range that some published power calculations use. In health outcomes at the village level, ICCs for infant and child anthropometrics run between 0.05 and 0.15. For self-reported behavioural outcomes — contraceptive use, hand-washing practice, latrine ownership — ICCs are often higher, in the 0.15-0.30 range, because these outcomes reflect community norms as much as individual choice.
The consequence of using an ICC that is too low is direct. A trial designed with ICC = 0.02, cluster size = 20, and 30 clusters per arm is powered to detect a certain minimum detectable effect on a certain outcome. That same trial run with an underlying ICC of 0.10 is powered to detect an effect substantially larger than the MDE the pre-registration named. If the true effect is between the pre-specified MDE and the actual MDE under the higher ICC, the trial will fail to reject the null. The programme will be reported as ineffective. It may not be ineffective. It may simply have been the target of a study that could not detect the effect the intervention produced.
What is the corrective? Three practices, in ascending order of cost and value.
First, pull ICC estimates from the actual data source or from 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. UDISE+ carries school-level administrative outcomes. Extract the ICC from data close to your setting. Do not import it from a published paper without checking.
Second, run sensitivity to ICC in the power calculation. Report the sample size needed to achieve the target power at ICC = 0.05, 0.10, 0.15, and 0.25 for the outcomes of interest. The four numbers tell the funder and the pre-registration reader what the trial is committing to. A single-point estimate hides the model uncertainty; the sensitivity table makes it legible.
Third, budget for a real baseline. A pilot survey of five to eight clusters, done early in the trial timeline, produces an in-sample ICC estimate for the actual outcome variable at the actual measurement frequency. It is the only way to know the ICC will be close to whatever the assumption was. In our experience, ICC estimated from a genuine pilot in the sampled population is meaningfully different from ICC lifted from external sources about seventy per cent of the time. The pilot is cheap by comparison to the trial. Trials that skip it are not saving money; they are shifting risk into the endline.
One further note on cluster size versus number of clusters. Given a fixed budget, the marginal power gain from adding one more cluster is much larger than the gain from adding one more observation within an existing cluster. This is a basic consequence of the design effect and it is under-appreciated in field practice. When budget conversations settle on "more surveys per village to reduce cost per interview," the resulting design is usually less powerful than the same budget spent on fewer surveys spread across more villages. Which trade-off is right depends on the ICC. Which is another reason to know it.
Pre-registration standards require reporting the ICC assumption. Journal reviewers rarely check it against the empirical distribution the outcome would sit in. If your trial reports ICC = 0.02 for a foundational-literacy outcome at the school level in India, you are asking the reader to accept a value that is one order of magnitude below the plausible range. Sometimes that is correct. Usually it is a convention that has drifted from what the data actually says.
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.