School Phone Bans: They Work on Phone Use, and the Learning Gains Keep Shrinking

This is one of the fastest-moving evidence bases in this whole field, and it has moved in one direction: away from the confident version of the story.

The 2016 study that started the policy wave found an effect significant only at the 10% level, concentrated entirely in the lowest-achieving pupils, from a survey with a 21% response rate. A better-powered Swedish replication found a null precise enough to rule out gains above 1% of a standard deviation. And the largest and best-designed test ever run - pre-registered, nationwide, using physically locked pouches - verified that the policy worked mechanically and still found test-score effects indistinguishable from zero.

What survives is narrower, real, and worth knowing.

The study that started it

Beland and Murphy (2016), in Labour Economics, examined 91 schools and 130,482 students across Birmingham, Leicester, London and Manchester, 2001-2011, using a difference-in-differences design on the timing of each school’s own decision to ban phones.

The headline effect was 0.0641σ (SE 0.0373) - significant only at the 10% level. The abstract rounds it to “about 0.07 standard deviations.”

The distribution matters more than the average:

Prior achievement quintile	Effect	Significance
Q1 (lowest)	0.1423σ (SE 0.0404)	p < 0.01
Q2	0.0986σ (SE 0.0401)	p < 0.05
Q3	0.0654σ (SE 0.0409)	n.s.
Q4	0.0229σ (SE 0.0409)	n.s.
Q5 (highest)	-0.0254σ (SE 0.0429)	n.s.

The authors’ own words: “students in the top quintile are neither positively nor negatively affected by a phone ban.”

Note the response rate: 21%, on a voluntary survey asking schools about their own phone policy. That is a selection problem, and it is the reason the replication matters.

The replication

Kessel, Hardardottir and Tyrefors (2020), in Economics of Education Review, deliberately mirrored that design in Sweden with 1,086 responding schools out of 1,423 - a 76% response rate - and 16,724 school-year observations across two decades.

Outcome	Effect	95% CI
Merit points	-0.042 (SE 0.025)	[-0.092, 0.008]
National maths test	-0.025 (SE 0.038)	[-0.100, 0.049]
Percentage failing maths	0.027 (SE 0.542)	[-1.036, 1.090]

This is not an underpowered null. The authors state they can reject effect sizes of the magnitude Beland and Murphy reported, and for merit points can rule out positive effects larger than about 1% of a standard deviation.

Their conclusion, verbatim: “while introducing a mobile phone ban is tempting due to its low-cost nature, such a ban should not be expected to produce substantial gains in student performance.”

The strongest test yet run

Allcott, Baron, Dee, Duckworth, Gentzkow and Jacob (2026), an NBER working paper, evaluated Yondr locked pouches across 1,778 adopting schools against 42,919 never-adopters, 2018-2025, using staggered difference-in-differences with a public pre-analysis plan.

The treatment worked. Teacher-reported in-class phone use fell from 61% to 13% - about an 80% decline. GPS pings fell. Teacher satisfaction with the policy rose from 26% to 75%. This is not a study of a policy nobody followed.

The achievement effects were essentially zero. Pooled combined score -0.006 (SE 0.010); maths -0.002 (SE 0.011); ELA -0.006 (SE 0.011). They can rule out improvements larger than about 0.007 student-level standard deviations.

Split by level, the picture is mixed rather than positive:

• High schools: maths +0.047 (SE 0.018), p < 0.05 - roughly 0.9 percentile points.
• Middle schools: combined -0.025 (SE 0.012), p < 0.05; maths -0.026 (SE 0.013), p < 0.05. Negative.

And the side effects are real. Suspensions rose about 15% in the adoption year (+0.078, SE 0.019), fading later. Student wellbeing followed a J-curve: -0.603 school-level SD in the adoption year, recovering to +0.485 and significant by two years later. Attendance was a precise zero. Online bullying: -0.039 (SE 0.092), not significant.

The most damaging detail for the theory: schools where phone use fell the most did not gain the most. That dose-response failure is not what you would see if the mechanism were real.

Why it cannot work, mechanically

Goodyear and colleagues (2025), the SMART Schools study in The Lancet Regional Health - Europe, is cross-sectional rather than experimental - which limits what it can prove - but it measured the thing that constrains the whole policy.

Restrictive schools did cut phone use during the school day: -0.67 hours of phone use (p = 0.00024) and -0.54 hours of social media (p = 0.00018).

And there was no difference in weekday or weekend totals. Pupils made every minute back after the bell.

The primary wellbeing outcome was null: adjusted mean difference -0.48, 95% CI -2.05 to 1.06, p = 0.62. The authors’ conclusion, verbatim: “There is no evidence that restrictive school policies are associated with overall phone and social media use or better mental wellbeing in adolescents.”

If wellbeing tracks total use, a school-hours policy cannot move it. That is the finding that explains all the nulls above.

What does survive

Three things, and they deserve to be stated as carefully as the nulls.

A small, delayed academic gain in older pupils. Figlio and Özek (2025), an NBER working paper using Florida administrative data (3,569,886 student-month observations for discipline), found test scores +0.62 percentiles (SE 0.28) in year two, rising to +1.08 (SE 0.45) for spring tests, and +1.42 (SE 0.48) for male students. Unexcused absences fell about half a percentage point. That is the same order of magnitude as Allcott’s high-school maths result, from an independent team using a different design.

A genuine randomised result. Sungu, Choudhury and Bjerre-Nielsen (2025), a working paper, randomised roughly 17,000 students across 10 higher-education institutions in India to lecture-time phone collection. Effect: +0.07σ on grades, roughly double for lower-performing students. Null on wellbeing, motivation and digital usage. This is the only randomised trial in the area - and it is on university students in lectures, not schoolchildren all day.

Bullying and girls’ mental-health service use. Abrahamsson (2026), now published in the Journal of Human Resources, studied 477 Norwegian schools and 161,371 student observations. Bullying fell for girls at full exposure (-0.42σ, p = 0.039) and for boys at four years (-0.39σ, p < 0.05). Girls’ specialist visits for psychological symptoms fell -2.7, p = 0.008 at three years.

Four qualifications belong with Abrahamsson. Full-sample effects on education and mental health are null - the headline results are a girls-only subgroup. GPA for girls at one year is +0.08σ, p = 0.064 - not significant at 5%. Several headline results sit between p = 0.058 and p = 0.094. And many of the “bans” were lenient - phones allowed at breaks, silent during lessons - rather than confiscation.

What nobody has done

There is still no randomised controlled trial of a whole-school phone ban on school-age children anywhere in this literature. A 2024 scoping review of 22 studies across 12 countries said so; it remains true.

That review’s conclusion: “little to no conclusive evidence that ‘one-size-fits-all’ mobile phone bans in schools resulted in improved academic outcomes, mental health and wellbeing and reduced cyberbullying.” Notably, two of its included studies found higher online victimisation in schools with restrictions.

The mechanism usually offered for bans has also failed its own test. Hartanto and colleagues (2024) meta-analysed the “mere presence” effect across 166 effect sizes, 53 samples, 33 studies and 4,368 participants: d = -0.02, 95% CI [-0.06, 0.01], p = .246. The idea that a phone in the room drains attention by sitting there does not survive pooling.

A note on how this reached you

UNESCO’s 2023 Global Education Monitoring Report is routinely reported as calling for a global ban. Its actual framing is conditional - technology should be used “only when it enhances learning” - and it concedes that limiting phone use “does not remove the need for students to learn how to navigate digital environments.”

The learning claim in its associated material is attributed to a study covering Belgium, Spain and the United Kingdom that the published blog does not name or cite. We could not identify it with confidence and are therefore not reporting its findings. The Spanish component appears to be a two-region synthetic-control study whose effect sizes are an order of magnitude larger than anything else in this literature; we have not printed those figures either.

A UN body’s conditional recommendation became a global mandate in the wire copy. That is worth knowing when you read the next headline.

What this leaves you with

Bans reliably do one thing: they reduce phone use in school. That is well measured and not in dispute.

They do not reliably improve attainment. The best-powered test rules out gains above 0.007 student-level SD, and found negative effects in middle schools.

They may help older and weaker students, slightly, on a delay. Two independent quasi-experiments and one RCT converge on something like 0.07σ or about one percentile point, appearing in year two.

They plausibly reduce bullying, though the strongest result is a subgroup finding in a study whose full-sample effects are null.

They cannot move overall wellbeing, because they do not change how much time a teenager spends on a phone.

Nothing here is a recommendation about school policy. This article reports what has been measured. Decisions about any particular school involve considerations this evidence does not address.

For what device use does to learning in a lecture hall - a different setting, a different device and a different literature - see laptops in the classroom. For the measurement problem underneath all screen-time claims, see is screen time accurate. For what phone presence does and does not do to attention, see check your phone less.

Limitations of this article

Two of the strongest studies are working papers, not peer-reviewed. Allcott and colleagues and Figlio and Özek are NBER working papers; Sungu and colleagues is an SSRN working paper. We label them as such and do not present them as published.

We did not print the Sungu effect size from the paper itself. The 0.07σ figure and the “double for struggling students” description come from the authors’ project page and a university publication, not from the working paper, which we could not open. Treat it accordingly.

We could not obtain the SMART Schools secondary-outcome estimates with confidence intervals. We print the primary outcome and the phone-use results, and describe the secondaries as the authors do.

We did not identify the study UNESCO cites for its learning claim, and have therefore reported nothing from it.

We did not print the Spanish synthetic-control effect sizes, which we could not read in the paper and which are far outside the range of the rest of the literature.

Allcott and colleagues operate under a data use agreement with Yondr, the company whose product they evaluate, and thank named company staff. Their analysis was pre-registered and their findings are unfavourable to that company, but the relationship belongs in the record. Their funders include Arnold Ventures, the Bezos Family Foundation, the National Governors Association, Stanford Impact Labs, the Stuart Foundation and the Walton Family Foundation.

A published critique of Abrahamsson exists as a blog post, not a peer-reviewed comment. We verified three of its four claims directly against the paper and have incorporated them; we attribute none of them to a peer-reviewed source.