The fifteen-year null.

In 1994, the Department of Housing and Urban Development set out to answer a question that had been argued in American social science for thirty years without resolution: do poor neighborhoods make people poor, or do they simply collect people who are already poor?

The question mattered enormously for policy. If concentrated poverty causes bad outcomes — through schools, peers, crime exposure, job networks, environmental stress — then moving families out is a powerful intervention. If concentrated poverty merely reflects who ends up living where, then moving families is expensive and pointless, and the money belongs in schools or jobs programs instead.

Observational data could not settle it. Families who move to better neighborhoods differ from families who don't in every way that also predicts their outcomes: motivation, health, family stability, information, and money. Every correlation between neighborhood and outcome was hopelessly confounded with selection.

So HUD ran an experiment.

The design

Moving to Opportunity for Fair Housing recruited 4,604 families living in public housing in census tracts where at least 40% of residents were below the poverty line, across five cities: Baltimore, Boston, Chicago, Los Angeles, and New York.

Families were randomly assigned to one of three groups. The **experimental group** received a housing voucher that could only be used in a census tract with a poverty rate below 10%, along with counseling to help them find and lease a unit. The **Section 8 group** received a conventional, unrestricted housing voucher. The **control group** received no voucher and kept their existing public housing assistance.

The design was careful about the thing that usually ruins housing research. Randomization broke the link between family characteristics and neighborhood quality. Whatever differences appeared later could be attributed to the neighborhood, because nothing else about the families differed systematically.

Take-up was the first complication. Roughly 48% of families offered the restricted voucher managed to actually lease a unit in a qualifying low-poverty tract within the time limit. Finding a landlord willing to accept a voucher, in a neighborhood the family had no connections to, with a deadline, turned out to be hard. This meant the experiment measured the effect of *being offered* a restricted voucher, which is a diluted version of the effect of *moving*.

What the evaluations found

The interim evaluation, published by Kling, Liebman, and Katz in *Econometrica* in 2007, and the final evaluation led by Sanbonmatsu for HUD in 2011, reported a consistent and deflating picture.

The intervention clearly worked at doing what it was designed to do. Families in the experimental group ended up in dramatically safer, less poor neighborhoods. They reported feeling safer. And their health improved in measurable ways — reductions in psychological distress and depression among adult women were substantial, and there were improvements in markers of extreme obesity and diabetes.

But on the outcomes the policy debate cared most about, there was nothing. Adult employment: no significant effect. Adult earnings: no significant effect. Welfare receipt: no significant effect. Children's test scores in the interim evaluation: no significant effect.

The verdict was widely absorbed as a refutation. The most rigorous test ever conducted of the neighborhood-effects hypothesis had moved thousands of families into better neighborhoods and produced no economic mobility. For roughly fifteen years, MTO was the canonical citation for the claim that place-based interventions do not work.

What the tax records showed

In 2015, Raj Chetty, Nathaniel Hendren, and Lawrence Katz did something the original evaluations could not have done: they linked MTO participants to federal income tax records, and looked at the children.

The timing is the whole story. The final evaluation reported in 2011, when many of the children who had moved as small children were still teenagers. Their adult earnings did not yet exist to be measured. The study had asked about economic mobility and then, necessarily, measured it on the adults — the parents — who had spent their entire formative lives in the old neighborhood before the experiment ever touched them.

By 2015 the children had grown up. The pattern in the tax data was sharp and it depended almost entirely on one variable: how old the child was at the time of the move.

Children who moved to a low-poverty neighborhood **before about age 13** earned roughly 31% more in their mid-twenties than children in the control group — on the order of $3,500 more per year. They were significantly more likely to attend college, attended better colleges, were less likely to become single parents, and lived in better neighborhoods themselves as adults.

Children who moved as **adolescents**, after roughly age 13, showed no such gains. If anything the point estimates ran slightly negative — plausibly the cost of disrupting a teenager's school and social network at exactly the wrong moment, without leaving enough years in the new environment to recover the investment.

The gains scaled with years of exposure. Each additional childhood year in a lower-poverty neighborhood contributed to adult outcomes in a roughly linear way. Neighborhoods were not a switch that flipped a family's trajectory. They were a dosage that accumulated across a childhood.

Why the first answer was wrong

It is worth being precise about the nature of the error, because it was not a mistake in execution. MTO was randomized, well-powered for its primary outcomes, carefully implemented, and honestly reported. Nothing about the original evaluations was sloppy.

The error was in the **measurement window**. The study's outcomes were measured on a timescale of four to ten years, on a population that included adults for whom the intervention arrived decades too late. The mechanism through which neighborhoods actually operate — accumulated childhood exposure, compounding into education and then into earnings — takes twenty years to become visible in the data. The evaluation reported at year fifteen and concluded, correctly given what it could see, that there was nothing there.

This is a general hazard, and it is under-appreciated. An experiment can be internally valid, adequately powered, transparently analyzed, and still deliver a confidently wrong answer if the outcome is measured before the mechanism has had time to produce it. Statistical rigor does not protect against a mistimed clock. Nothing in the standard toolkit — power calculations, pre-registration, robustness checks — flags the problem, because all of them take the measurement window as given.

Project STAR, the Tennessee class-size experiment, has the same shape. Its test-score effects faded within a few years of students returning to normal classrooms, and for a period this was read as evidence that class size did not durably matter. When Chetty and colleagues later linked STAR participants to tax records, the students assigned to small classes showed higher college attendance and earnings as adults. Two landmark education and housing experiments, both initially read as disappointments, both reversed by administrative data twenty years later.

What changed in practice

The revised finding did not stay academic.

The exposure-time result implied something specific and actionable: the return on housing mobility is concentrated in families with young children, and the binding constraint is not the voucher but the move. MTO had already shown that fewer than half of families offered a restricted voucher managed to use it. The barrier was search — finding units, reaching landlords, navigating a rental market in an unfamiliar part of the city, all under a deadline.

Creating Moves to Opportunity, run in Seattle and King County by Bergman, Chetty, DeLuca, Hendren, Katz, and Palmer, tested whether attacking that constraint directly would work. Families received customized search assistance: help identifying units in high-opportunity areas, landlord recruitment, short-term financial help with application fees and deposits, and a navigator to work through problems as they came up.

The share of families leasing in high-opportunity neighborhoods rose from about 15% to about 53%. It was a large effect from an intervention that added no new housing subsidy — it only made the existing one usable.

What to take from it

Three things.

**First, a null result is a statement about a measurement, not about the world.** MTO did not find that neighborhoods don't matter. It found that neighborhoods did not measurably change the earnings of adults within a decade — which, in retrospect, is exactly what the exposure-time model predicts. The finding and the interpretation drifted apart, and the interpretation is what shaped fifteen years of policy.

**Second, the measurement window is a design parameter and deserves the same scrutiny as sample size.** Before running an evaluation, it is worth asking explicitly: through what mechanism should this work, how long does that mechanism take, and will my study still be looking when it arrives? If the honest answer is no, that needs to be stated at the outset — not discovered by someone else two decades later.

**Third, administrative data changes what is knowable.** Neither the MTO reversal nor the STAR reversal required a new experiment. Both required linking old randomized assignments to tax records that already existed. Every well-randomized experiment is a permanent asset, and its most important finding may be recoverable long after the study has closed. That is an argument for preserving assignment records with care — and for treating the final report as a milestone rather than the end.