How We Know What Changed After Reinstatement
The central empirical question is whether reinstating SNAP’s ABAWD work requirement changed work or mainly changed access to SNAP. The 2026 study addresses that question with linked administrative records and a comparison built from age, geography, and timing. Understanding the design matters because a simple before-and-after comparison could mistake a changing labor market, a different age group, or a different county for the effect of the rule itself. The result is not a direct national experiment, but it is more informative than a caseload chart taken on its own.
The study also gives readers a useful lesson in how evidence should be read. It reports several estimates, but it does not treat them as equally persuasive. The preferred triple-difference estimate is the main guide for the labor-market result because it removes more shared sources of change and avoids visible pre-trends that affect some alternative comparisons.
The comparison is built in layers
The sample begins with people who received SNAP while ABAWD requirements were suspended. The researchers focus on childless adults aged 45 to 55. They use ages 45 to 49 as a proxy for the group subject to the ABAWD requirement and ages 50 to 55 as a comparison group generally exempt from it. The age bands are close enough to make a comparison plausible, but they are not identical. The younger group may differ in employment trends, health, earnings, or other characteristics that change with age. That is why age alone cannot identify the effect.
The researchers add geography. In five states with partial reinstatements, some counties or comparable local areas reinstated the ABAWD requirement while other areas in the same states retained waivers. The treated group is therefore defined by two conditions: being in the younger age band and living in an area where the requirement became active. The comparison group includes people in the older age band and people in areas where a waiver remained. The paper also uses a broader difference-in-differences design covering all nine states in the administrative sample, including states that reinstated the rule statewide.
Finally, the researchers add time. They observe outcomes before and after reinstatement, following people for up to 18 months after the change and using pre-period observations to test whether the groups were moving in parallel before treatment. The question is not merely whether younger adults in reinstated counties had a different participation rate than older adults in waiver counties. It is whether the difference between those groups changed after the rule became active, relative to the change in places where the rule did not become active.
This is the intuition behind a triple difference. One difference compares the period before reinstatement with the period after it. A second compares adults near but below the age cutoff with adults just above it. A third compares areas where the rule was reinstated with areas where waivers remained. A common shock affecting everyone—such as a national change in food prices—can be removed by the time comparison. A general age-related trend can be removed by comparing the age groups. A local shock shared by both age groups in the same area can be removed by comparing reinstated and waiver areas. The method does not eliminate every possible problem, but it asks more of the data than a single before-and-after line.
The identifying assumption is a counterfactual one: without reinstatement, the difference between the younger and older groups would have evolved similarly in reinstated and waiver areas. The paper examines this with event-study estimates that show how the gap moves month by month or quarter by quarter. If the gap is already widening before the policy starts, a later difference may be a continuation of that trend rather than an effect of reinstatement. Parallel pre-trends do not prove the assumption, but visible violations make the comparison less credible. This is why the design choice matters most for employment: the alternative age-only comparison shows a pre-trend, while the preferred geographic comparison removes it.
The fixed effects in the statistical model implement the same logic in a more formal way. Age-by-county effects absorb stable differences between age groups across places. Age-by-time effects absorb changes that affect one age group across all locations. County-by-time effects absorb local shocks shared by both age groups. The remaining treatment estimate is not “the difference between younger and older adults”; it is the residual change associated with being in the younger group, in a reinstated area, after the rule became active. Readers do not need the equation to use the idea, but they do need to know what kinds of variation the estimate is trying to remove.
The employment and earnings records add another important feature. SNAP records show participation, benefit amounts, income, and demographics. The linked Longitudinal Employer-Household Dynamics records show whether a person had any UI-covered employment in a quarter and, for four states, the earnings associated with covered jobs. The linkage makes it possible to ask whether a person left SNAP and appeared in observed employment, rather than inferring work from benefit status.
It also creates boundaries. Informal work, employment not covered by the records, and later outcomes may not appear. ABAWD status is proxied because the administrative files do not consistently record it and disability information is incomplete. The proxy may include some people who would not legally be subject to the rule and can therefore dilute the measured effect. A strong design is not the same as a complete view of every pathway.
The outcome definitions matter as much as the comparison groups. SNAP participation is a monthly indicator, so a person who misses a month and later returns can contribute a different pattern from a person who leaves for the rest of the observation window. Average benefits include zeros for people who are no longer receiving SNAP, which makes the benefit decline combine two changes: the amount paid to continuing participants and the number of participants receiving anything at all. Employment is an indicator for any UI-covered job in a quarter, not a measure of hours, job quality, stability, or whether the work was sufficient to replace food assistance. Earnings are quarterly totals in the states where those data are available. These measures are appropriate for the questions the study can observe, but they should not be stretched into claims about every dimension of economic well-being.
What the design finds
The event-study pattern for SNAP participation is consistent with the institutional rule described earlier. Before reinstatement, the preferred comparison does not show a clear divergence in the relevant age-and-area difference. After reinstatement, participation drops around three months later, matching the period in which ABAWDs begin to lose benefits if they have not satisfied the condition. The gap narrows somewhat but remains substantial through the follow-up period.
The preferred triple-difference estimate puts the participation decline at 4.4 percentage points, about a 7 percent reduction relative to the pre-reinstatement mean. Average SNAP benefits, counting people who no longer receive benefits as zero, fall by about $8 per person in that estimate. These numbers describe the effect for the partial-reinstatement sample and its comparison structure. They are not a forecast that every SNAP recipient nationwide would experience the same percentage change under any future law.
The labor-market result is different. The preferred DDD estimate for employment is a small -0.4 percentage points and is not statistically significant. The paper’s 95 percent confidence interval rules out effects larger than a 1-point decline or a 0.2-point increase within the measured outcome and sample. Quarterly earnings, available for only four states, show an insignificant reduction of about $15; the confidence interval rules out a decline greater than $54 or an increase greater than $23. In ordinary language, the preferred design does not find a meaningful positive employment or earnings response.
That statement needs two qualifications. First, “not statistically significant” does not prove that the true effect is exactly zero. It says that the estimate is too uncertain, or too close to zero, to support a detectable positive effect within the study’s bounds. Second, an aggregate estimate can conceal individual movement. Some people may have worked more, while others lost benefits without finding work. The average result tells us that any positive responses did not produce a robust net increase in the measured employment outcome.
The alternative DiD estimates illustrate why comparison design matters. In the same partial states, the DiD estimate shows a 5.7-point participation decline, or about 9 percent. In the all-state sample, the decline is 8.7 points, or about 13 percent. Those estimates are useful descriptions of alternative samples, but the paper identifies a clear pre-trend in the DiD employment comparison: the older group was already moving differently from the ABAWD-age group before reinstatement. A positive post-reinstatement coefficient can therefore reflect a pre-existing difference rather than a causal work response. The authors rely on the DDD specification for employment because adding the geographic comparison removes that pre-trend in the preferred analysis.
This is not a technical dispute with no practical meaning. If the comparison group is already on a different employment path, a post-policy increase can be falsely attributed to the requirement. Conversely, a carefully chosen comparison can show that a dramatic access change did not coincide with a meaningful labor-market change. Method determines which interpretation the evidence can carry.
The preferred design still has limits. The comparison relies on adults close in age being sufficiently similar after the model accounts for observed patterns. County waiver status may be related to labor-market conditions, and those conditions can change over time. The paper’s use of never-treated or waiver areas helps, but it does not turn the study into a randomized assignment. The most defensible claim is therefore conditional: among the selected childless adults in the reinstatement settings, under the design’s identifying assumptions, participation fell and the preferred labor-market response was not detectable.
Reading the newer result beside earlier evidence
CBO’s 2022 report summarizes earlier studies that compared adults near age 50 in several states. Those studies estimated employment gains of roughly 1 to 4 percentage points for the older ABAWD-age workers, while finding much larger participation declines in some states. CBO therefore concluded that the SNAP work requirement probably increased employment for some people but reduced average income overall because the benefit losses were larger than the earnings gains for the group as a whole.
The CBO and Census conclusions should not be compressed into a single average. The CBO report is a broader synthesis of evidence available at that time. Its studies cover different states, labor markets, enforcement systems, and periods. The 2026 paper uses newer linked administrative records and a preferred DDD design across selected reinstatement settings. Its authors also compare their estimates with earlier literature and explain why they discount alternative DiD labor estimates with pre-trends. The later result may be more informative for the settings it studies, but it does not automatically invalidate evidence from a different state or population.
What survives the comparison is more stable than the disagreement about employment size. Both sources treat participation loss as a central effect of the ABAWD rule. Both indicate that the loss of benefits can exceed the earnings response for many affected people. The remaining uncertainty concerns how much employment the rule creates in particular environments, not whether leaving the rolls is itself proof that work was created.
The design also tells us what additional evidence would change the judgment. A stronger positive employment result would need to appear in a comparison without the pre-trend problem, using a measure that captures the relevant work and a population for which the rule is actually active. Evidence about informal work or longer-run earnings could qualify the short-run administrative result. Evidence showing that effects differ sharply by local labor demand, wages, exemptions, or access to training would not erase the participation estimate; it would explain where the employment response is more or less likely.
The main lesson is therefore methodological and substantive at once. Reinstatement gives researchers a policy change with observable timing, but the effect is identified by the structure of the comparison, not by the policy label. In the preferred evidence, access falls clearly, while a meaningful labor-market gain is not detected. The next question is no longer whether the two outcomes are different. It is what mechanisms—barriers, local opportunity, documentation, and feasibility—can produce that divergence.