The Impact of Cellphone Bans in Schools on Student Outcomes: Evidence from Florida

One large urban county-level Florida school district ("LUSD"), student-level administrative records for school years 2022-23 through 2024-25; test scores observed three times per year and disciplinary incidents daily; Advan mobile-device data covers more than 95% of the district's students' school buildings.

K-12 students in a single large urban Florida district, elementary through high school. The district's policy is stricter than Florida's statewide law — phones must be silenced and stored all day, not merely during instructional time.

A novel and clever identification strategy, which is also its main vulnerability. Since the ban hit every school in the district at once, there is no untreated comparison group in the usual sense. Instead the authors measure how much each school's cellphone activity FELL when the ban took effect, using building-level smartphone-location data from Advan (comparing regular school days against teacher in-service days, when pupils are absent), and run difference-in-differences comparing high-effect schools (where student phone use dropped a lot) against low-effect schools (where it did not). The assumption is that only high-effect schools were meaningfully treated; the authors present evidence that the Advan contrast reflects student rather than staff phone use, and event studies show no differential pre-trends. STRENGTHS: administrative records at unusually high frequency, nationally normed test scores rather than researcher instruments, three separate outcome families (achievement, discipline, attendance), and — rare in this cluster — an explicit DISPLACEMENT measure. WEAKNESSES: a single anonymous district, so external validity is untested; the treatment intensity measure is constructed from commercial foot-traffic data and is new enough that its properties are not independently established; high- and low-activity schools differ in ways (student composition, ownership rates) that the DiD assumes are trend-parallel rather than level-equal; the paper is an NBER working paper that has not been peer reviewed; and the effects are small in absolute terms (0.6 to 1.4 percentiles). The district supplied the data and gave feedback; the authors are at the University of Rochester and RAND and the work was funded by the Smith Richardson Foundation, so this is independent of any device or software vendor. Graded C: credible quasi-experiment, single site, novel and unvalidated treatment measure, not yet refereed.

Banning phones in one large Florida district raised test scores modestly and only after an adjustment year, and it did so mainly by getting students to turn up. Test scores in high-effect schools rose about 0.6 percentiles overall in year two (1.1 percentiles on the high-stakes spring tests; 1.4 for boys, 1.3 for middle and high school students; nothing for girls or for elementary pupils). In year one the ban's visible effect was DISCIPLINARY, not academic: suspensions and disciplinary incidents rose about 12 percent of the comparison mean and in-school suspensions about 20 percent, driven overwhelmingly by Black students (about 30 percent) and by male students, with no significant effect for White or Hispanic students. Those effects disappeared in year two, which the authors read as an adjustment period settling into a new steady state. The finding this archive most wants recorded is the third: unexcused absences fell 5-10 percent of the comparison mean in middle and high schools, and an exploratory mediation analysis attributes NEARLY HALF the test-score gain to that attendance change. If that holds, the phone in a US high school is costing learning largely by keeping students out of the building, not by distracting them inside it — a completely different mechanism from the attentional story that Sana et al. and Beland & Murphy assume. The caveat that most changes how this should be read: one district, an untested treatment-intensity measure built from commercial location data, and a real equity cost in year one borne disproportionately by Black students.

Medium. Within-district difference-in-differences with school and time fixed effects, so student genotype does not change at the ban date; but treatment intensity is measured by pre-ban phone use, which correlates with student composition, so the high- vs low-effect contrast is not a random assignment of children.

Added to this cluster because it is the first US causal evidence on cellphone bans and because it breaks the Beland & Murphy / Kessel deadlock in an unexpected direction — not by picking a side but by finding a MECHANISM neither of them measured. It corroborates Beland & Murphy (`edt-beland-murphy-2016-ill-communication`) on the existence of a test-score gain, but not on its shape: gains here appear only in year TWO, are larger for boys and for White students, and are absent for elementary pupils, whereas Beland & Murphy's were concentrated in the lowest-achieving quintile regardless of sex, and Abrahamsson's (`edt-abrahamsson-2024-smartphone-bans-norway`) were confined to girls. Three studies, three incompatible heterogeneity stories, is the honest summary of the subgroup literature. It contradicts Kessel's precise null (`edt-kessel-2020-phone-ban-sweden`), though Kessel's own explanation — that Sweden had already structured its device use, leaving little unstructured phone use to remove — is consistent with a US district finding an effect. This is an unrefereed NBER working paper as of the date of this record.