Randomised controlled trials did not originate in behavioural economics. They arrived there from development studies, carried by researchers who needed credible causal estimates in places where administrative data was thin. The method changed both fields, and it also carried a critique that has never been settled: that trials answer narrow questions well while crowding out the structural ones.

The Method That Jumped Disciplines

Development economics in the early 2000s faced a credibility problem. Cross-country regressions could not isolate cause from confound, and programme evaluations often compared participants with whoever happened to be nearby. Esther Duflo and Abhijit Banerjee, working with colleagues at MIT and later through the Abdul Latif Jameel Poverty Action Lab, pushed randomisation as the default for testing anti-poverty programmes. Their early work on teacher incentives, deworming, and microfinance became the template.

Behavioural economists watched closely. The questions were familiar, about how people respond to incentives, defaults, and framing. What was new was the willingness to run the trial in the field rather than the lab. By the 2010s, teams in several rich countries were running randomised trials on tax reminders, energy bills, and job-search support. The designs were borrowed almost wholesale from development work.

The direction of travel matters. Lab experiments in behavioural economics had long relied on undergraduate pools and modest stakes. Field trials offered real decisions with real money, and the trade-off was control. A lab can hold everything constant. A field site cannot. Development researchers had already learned to live with that trade-off, and their habits travelled with the method.

Why Development Studies Built the Toolkit

Weak infrastructure forced the issue. In settings where tax records were incomplete and household surveys were expensive, randomisation was often the cheapest credible identification strategy available. A lottery for a scholarship or a bed net distribution could generate a comparison group at almost no extra cost. That logic was not primarily about behavioural science. It was about making causal claims defensible.

Poverty programmes also demanded measurable outcomes. Donors wanted to know whether a cash transfer improved school attendance or a training scheme raised earnings. Randomised trials answered those questions in a form that survived scrutiny. The J-PAL network, founded in 2003, spread the template across dozens of countries and trained a generation of researchers in the same design conventions.

There were costs. Trials are slow, and they answer narrow questions well. A study might show that a particular incentive raised attendance in a particular district without saying much about why. Critics inside development economics argued that the method crowded out structural questions about markets and institutions. That argument never fully resolved, and it followed the method into its new home.

What Changed When It Arrived

Rich-country policy labs adopted the trial as a governing tool. The Behavioural Insights Team, set up inside the UK government in 2010 and later spun out as a social purpose company, ran dozens of randomised trials on public services. Nudge units appeared in the US, Singapore, and elsewhere. The pitch was simple: test small changes before rolling them out at scale.

Effect sizes told a sobering story. A widely cited synthesis by Benartzi and colleagues in 2017, covering more than 100 trials, reported average effects of roughly 0.1 to 0.2 standard deviations, with wide variation. Some interventions, like simplified letters to encourage tax payment, showed larger movement. Others barely registered. The development literature had already reported a similar spread, from near-zero to substantial, and the new field reproduced it.

Sample sizes grew. Where a development trial might randomise a few hundred villages or schools, a government trial could draw on tens of thousands of households through administrative records. Bigger samples bought precision, not necessarily larger effects. They also made it easier to detect small effects that might not matter much for policy.

The method also changed the questions asked. Behavioural teams tended to focus on individual decision-making, defaults, and messaging, because those were the levers a policy unit could pull. Development researchers had often studied the same levers in the context of poverty. The overlap was real, but the framing shifted toward behaviour and away from structural constraints.

The Replication Reckoning

Replication efforts arrived with the method. In psychology, the Open Science Collaboration's 2015 project re-ran 100 published studies and found that only about a third reproduced the original significance, with effects often half the size. In economics, Camerer and colleagues' 2016 replication of 18 laboratory experiments in top journals found a similar pattern: effects roughly two-thirds the original magnitude on average. Publication bias and selective reporting explained part of the gap. Early estimates had been inflated by the practice of publishing the most striking result from a set of analyses.

Pre-registration became standard practice in response. Researchers began filing their hypotheses, sample sizes, and analysis plans before collecting data. Journals and funders adopted the requirement unevenly, but the norm shifted. Development labs were early adopters, partly because their trials were expensive and slow, and partly because the credibility of the whole enterprise depended on it.

Funding moved toward larger confirmatory trials. A single small study was no longer enough to justify a national rollout. Funders wanted replication in a different population, or at least a pre-registered design with enough power to detect a modest effect. The change was not universal, and plenty of underpowered trials still get published. The bar moved, though.

There is a live disagreement about how much the reckoning cost. Some researchers argue the field overcorrected, treating any non-replication as evidence of fraud rather than noise. Others say the correction was overdue and incomplete. Both positions have evidence behind them, and the argument is not settled. A related pattern shows up in other fields, where a 2016 reanalysis reversed a pain study's effect after the original blinding log was found to mismatch.

The Structural Critique

The most persistent objection to the method's migration is that it narrows the questions economics asks. A trial can tell you whether a reminder letter lifts tax compliance or whether a coaching programme shortens unemployment spells. It cannot easily tell you why unemployment is high, how labour market institutions shape job quality, or whether a different tax system would produce better outcomes than a nudge. Those are structural questions, and they require different methods: natural experiments, historical analysis, comparative institutional work.

Critics argue that the prestige and funding attached to randomised trials have pulled young researchers away from structural work. A graduate student who can run a clean field trial has a clearer path to publication and grants than one working on industrial policy or market design. The result, on this view, is a discipline that has become very good at estimating small effects of small interventions while losing capacity to analyse the large forces that set the context for those interventions.

Defenders respond that the critique romanticises a period when structural claims were often untestable and frequently wrong. Better to know a modest effect precisely than to assert a grand one loosely. They also note that many structural questions can be approached with experimental methods, through phased rollouts or policy lotteries, and that the boundary between the two styles is less sharp than the debate suggests.

The disagreement is not resolvable by more data of the same kind. It turns on what economics is for, and on which questions deserve the field's scarce attention. That argument has been running since the method arrived, and it shows no sign of closing.

Where the Traffic Flows Now

Development labs still dominate global randomised trial counts. J-PAL affiliates have run hundreds of evaluations, and the network's training programmes continue to supply researchers to governments and NGOs. The institutional centre of gravity remains in development, even as behavioural teams in rich countries run high-profile trials of their own.

Methods do travel back. A concrete case is the use of behavioural insights in development programme design: the World Bank's Mind, Behavior, and Development Unit, launched in 2015, applies findings from rich-country behavioural research to development projects, such as designing savings commitment products for low-income households. The traffic is not one-way, but it is uneven.

Scaling remains the hard part. A trial that works in a few hundred schools may not survive a national rollout, because the conditions that made it work change. Policy teams have learned to run phased rollouts with randomisation built in, which turns implementation itself into an experiment. That approach is expensive and slow, and it is also the only way to know whether an effect holds at scale.

The method serves whoever can afford the sample. Governments with administrative data and research budgets have an advantage. Smaller organisations often cannot run a credible trial, which shapes which questions get answered. That imbalance is a recurring complaint in the field, and it has no easy fix. It also connects to wider debates about how research gets funded, including grant renewals weighing preprint citation speed over experimental depth.

Practical Steps for Reading Trial Claims

Check for pre-registration before trusting an effect size. A trial with a filed analysis plan is harder to spin than one without, and the plan should match what was reported.

• Find out who funded and who ran the trial, since implementers with a stake in the result may shape the outcome measures.
• Look for replication in a different population, because a single-site result may reflect local conditions rather than a general rule.
• Read the sample size and attrition figures, since high dropout can quietly undo randomisation.
• Treat single-study results as provisional, especially when the effect is small and the policy stakes are high.