The impact of banning mobile phones in Swedish secondary schools

1,086 of 1,423 Swedish schools surveyed successfully (76% of schools; 16,724 of 22,832 school-year observations, 73%); 9,371 observations for national maths test scores and 12,760 for the maths failure rate. 631 schools (about 60%) had a ban by 2017.

Grade 9 leavers (age 15-16) in the universe of Swedish compulsory schools with at least 15 pupils, school years from 1997/98 to 2017/18. Both municipal and voucher schools.

Deliberately built as a same-design, different-country replication of Beland & Murphy. The authors surveyed every Swedish grade-9 school about whether and when it introduced a mobile phone ban, chasing non-responders by telephone until they hit a 76% response rate (against 21% in the original), and merged this with Statistics Sweden administrative data. Estimation is a staggered difference-in- differences with school and year fixed effects, robust standard errors clustered at the school level, plus a non-parametric event study with five leads and lags. Three outcomes: school-average merit points (grade 9 school-leaving certificate), average score on the national maths test, and share failing the national maths test; grades and test scores are standardized nationally by year exactly as in Beland & Murphy. Pre-trends are flat on all three outcomes. Validity checks relate ban adoption to seven other school-level policy variables (staffing, teacher qualifications, pupil-teacher ratio, and the timing of Sweden's one-to-one laptop rollout) and find no relationship, so the ban is not proxying for a general disciplinary or resourcing shift. LIMITATIONS, stated by the authors and important: (1) the data are SCHOOL-LEVEL AVERAGES, so the paper cannot directly reproduce Beland & Murphy's student-level heterogeneity by prior achievement — it substitutes quintiles of a school socioeconomic index, which is a weaker proxy; (2) adoption timing is still school-chosen, the same endogeneity that keeps the original off grade B, which is why this is also graded C despite far better sampling and precision; (3) merit points are teacher-set and known to be inflated in Sweden, which is why the externally marked national maths test is carried alongside; (4) the authors' own preferred explanation for the divergence — that Sweden's long, structured investment in school ICT (about 70% of grade-8 pupils already owned a computer) leaves little unstructured phone use to remove — is a plausible story offered without a direct test. Independent academic work (IFN Stockholm, Sodertorn, Stockholm University), funded by Swedish research foundations. Displacement was NOT measured. Numbers here were read from the full text of IFN Working Paper 1288 (version dated 2020-02-11), which is the accepted manuscript of the Economics of Education Review article; the publisher version is paywalled and was not consulted, so table numbering may differ from the journal version.

Banning mobile phones in Swedish schools did nothing, and the estimate is precise enough to say so. Merit points: -0.034 (SE 0.029), 95% CI [-0.092, +0.024]; adding the socioeconomic index gives -0.042 (SE 0.025) and the ability to reject positive effects above about 0.01 SD. National maths test scores: -0.025 (SE 0.038), CI [-0.100, +0.049]. Share failing maths: +0.027 percentage points (SE 0.542), CI [-1.04, +1.09]. Event studies show flat pre-trends and no post-ban step on any outcome. The result survives restricting to the four largest cities (to match Beland & Murphy's urban sample), excluding them, and truncating the panel to 2000-2012 and 2000-2014 to match the original's period. The one crack the authors report and then talk down: in the lowest quintile of the school socioeconomic index the ban is associated with +0.251 SD on maths test scores and -3.3 percentage points on the failure rate — the direction Beland & Murphy predict — but the authors caution that they estimated many specifications and the corresponding event-study plots show no convincing causal pattern. The caveat that most changes how this should be read: school-level averages cannot test the original's student-level low-achiever claim head-on, so what is definitively rejected is the AVERAGE effect, not every version of the heterogeneity story.

Medium. Within-school before/after design on the universe of schools, so pupil genotype is not what changes at the ban date. The socioeconomic-index quintile split is confounded in the usual way.

Direction of this record, stated plainly so the enum is not misread: THIS PAPER IS THE FAILED REPLICATION. Its authors set out to reproduce Beland & Murphy (2016; `edt-beland-murphy-2016-ill-communication`) with a better sample and could not. Their point estimate is NEGATIVE (-0.034 on merit points, SE 0.029) and the 95% confidence interval is [-0.092, +0.024], so the upper bound sits below Beland & Murphy's +0.064 — this is not an underpowered shrug, it is a precise rejection of an effect that size. With the socioeconomic index added the interval tightens further and the authors can reject positive effects larger than about 1% of a standard deviation. The `mixed` flag records the status of THIS paper's own finding (the null), not of the replication attempt. That null is corroborated by Abrahamsson (2024/2026, Norway), whose FULL-SAMPLE estimates on GPA, teacher grades and academic-track choice are also null — she says so explicitly and cites Kessel — and contradicted by Figlio & Ozek (2025, Florida), who find year-two test-score gains in a US district. The honest state of the literature is therefore a genuine disagreement across countries, and this archive leaves it standing rather than picking a winner.