In an RCT with multiple treatment arms, I heard that the "pure" control group be small to if we expect the effect size to be large. Why would this be the case? I understand that we could have a smaller sample if the effect size is expected to be large, but wouldn't we in any case be better off having 1:1:1 allocations?

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    $\begingroup$ In fact, you might want a larger control group when you have multiple arms that will be primarily compared to control because the control group is involved in all the comparisons and each other group is involved in only one. The ALLHAT trial is one example (note: not an untreated control): jamanetwork.com/journals/jama/fullarticle/195626 $\endgroup$ Commented Jun 17 at 20:21
  • $\begingroup$ the "pure" control group be small to if we expect is ungrammatical. Could you edit for clarity? $\endgroup$ Commented Jun 19 at 5:11

3 Answers 3


Power-wise, yes, a 1:1 comparison is going to be statistically optimal. There are several reasons why not all studies use balanced allocation however, by no means exhaustive:

  • The idea of being allocated placebo is not too attractive for investigators and their patients. Not having a control is usually out of the question for obvious reasons. You could argue that the most efficient and thereby most ethical study is a balanced one, but the truth is that people are motivated by the prospects of receiving investigative -- hopefully helpful but often unproven! -- drugs.
  • There might be other design considerations in play. Consider for example a dose-finding study, which should ideally also include doses that are suboptimal (no real benefit over placebo) or potentially at the upper edge of risk-benefit (lower doses comparably effective and safer) so that you can characterize the full dose range. You might want to include more subjects in those arms that have the highest predicted chance of success, in addition to the control arm. Another example could be a run-in where responders are re-randomized: you might not include many (or even any) controls here, since these are expected to respond less leading to lower efficiency in later design stages.
  • Control arms are often the lowest-hanging fruit for incorporating external or historical data, which then means you might require fewer actual subjects in your study here.

At the end of the day a clinical study is often a compromise between many competing design factors, of which statistics is a major but not the only one (and as I always say, we're not the ones paying the bill).

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    $\begingroup$ +1. As another design consideration, often you may want to run further analysis in the experimental group, maybe doing a subgroup analysis for example. If you have enough data to reliably answer the main research question of differences between arms, it can be beneficial to allocate remaining sample size to the arm you're really interested in, in order to sufficiently power follow-on analyses. You might need more samples to find a biomarker signature of response to the experimental drug, for example, while historical data tells you not to bother looking for markers of placebo response. $\endgroup$ Commented Jun 17 at 17:34

I don't know where you read this, so I don't know what their reason was, but one possible reason is ethical, rather than statistical.

If you expect the effect size to be large, then you will not need a huge sample to have sufficient power to find a significant difference, and it seems unethical to deny people treatment unnecessarily.


With multiple treatment arms that are being compared to a single control arm, the logic is a bit different than usually. In this situation, not a 1:1:...:1 allocation, but the square root allocation $1:1: ... :\sqrt{k}$ is statistically most efficient, where $k$ is the number of treatment arms.

This is still fewer patients allocated to control than if one would do separate 1:1 trials for each treatment. As others have commented already, this is attractive for investigators and patients, because controls are usually less exciting for business development and less promising for health benefits.

An intuitive understanding might follow from an example: in a platform trial, you may have 10 treatments, all being compared to a single control group, thus 10 comparisons. Assuming, you have allocated 100 patients to each arm, then you are comparing the 100 patients in the treatment arms each time against the same 100 patients of the control arm. Any random deviation from the truth in the control group will accumulate and inflate the error in the treatment effect estimate. It can be shown, that with the square root allocation, the standard error of the treatment effect estimate is minimized. As usually, assuming normal distributed outcomes and equal variances across groups - which is unrealistic, and therefore a lot of research on this topic is ongoing.

An early reference for this is Dunnett, C. W. (1955). A multiple comparison procedure for comparing several treatments with a control. Journal of the American Statistical Association, 50(272), 1096-1121.


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