Does any of this actually work? What the evidence says

The rest of this wiki is a manual.

It explains what every setting does.

It does not say whether the settings, taken together, do what parents hope they will.

This page says that.

It is the most honest article in the wiki.

It is also the shortest route to the editorial stance the rest of the wiki is built on — see ADR-0005 in the repository.

If a relative asked “does Screen Time, Family Link, or any of those parental-control apps actually work?”, this is the answer this wiki would want them to leave with.

Definition

A research-grounded review of what peer-reviewed studies and professional consensus documents have measured about technical parental controls — Screen Time, Family Link, content filters, monitoring apps, third-party tools — and about the non-technical family practices that travel alongside them.

It is not a product comparison.

It is not a recommendation to install, ignore, or remove a control.

It is a summary of what the evidence is and is not able to say.

Scope

This page covers ages roughly 6 to 16 — the wiki’s primary age band.

It reaches into the under-5 evidence where it is strongest [source: who-under5-2019] [source: publications-aap-digital-ecosystems-2026].

What is true about a 4-year-old’s screen exposure is also where the cleanest causal evidence sits.

It is built on a research pass that retrieved 36 sources across the evidence and guideline tracks as of 2026-08-16.

None of them are manufacturer claims.

Every cited study or guideline is either peer-reviewed scientific research, an institutional consensus, or a professional body statement.

Manufacturer materials are listed in the rest of the wiki as [claim] and do not appear here.

The page covers four questions:

1. What did the research actually measure?
2. Where do technical controls show a benefit?
3. Where do they not?
4. What consistently helps more than the controls themselves?

It does not cover what to do tonight if a child has already been exposed to a harmful contact.

That belongs on the emergency page.

Why this matters

Two thirds of parents of 6- to 13-year-olds in Germany use no technical controls at all [source: ADR-0005].

That is not a verdict against the controls.

It is a verdict against the way controls have been sold: as a single switch that fixes the problem, with no attention to what the research says they do.

The same synthesis that produced that number also produced the most careful recent estimate of what “digital parenting” — the umbrella term for the rules, conversations, co-use and technical controls a parent puts in place — actually moves in children’s outcomes.

Tan and colleagues pooled 88 primary studies from 2008 to 2024 and estimated a small negative association between digital parenting and children’s negative digital wellbeing [source: doi-tan-digital-parenting-2025].

The estimate was r = -0.05 with a 95% CI of -0.08 to -0.01, across 423 independent effect sizes.

Read carefully, that number means three things at once:

• It is a real association, statistically distinguishable from nothing.
• It is very small. The “r” scale tops out at 1.0. -0.05 is just past the threshold of detection.
• It is an association, not a causal effect. The studies that fed into it were predominantly cross-sectional — a snapshot, not a trial.

The same synthesis found no statistically clear overall association between digital parenting and positive digital wellbeing (r = 0.10, p = .10) or amount of digital use (r = 0.03, p = .34).

The authors also flagged possible publication bias for the negative-wellbeing findings [source: doi-tan-digital-parenting-2025].

That is the field’s best single estimate of what digital parenting in general — controls plus everything else — does on average.

It is the starting point for this page, not the conclusion.

What the research actually measured

The bulk of the evidence in this domain falls into four designs.

Each design answers a different question.

Reading a headline without knowing which design produced the headline is the most common mistake parents make with screen-time research.

Large cross-sectional surveys.

A representative sample is asked about media use and wellbeing at one point in time.

The researchers look for statistical associations.

The EU Kids Online survey covered 25,142 internet users aged 9 to 16 in 25 European countries and is the model for this design [source: basw-eu-kids-online-mediation-2012].

A later eight-country study by Livingstone and colleagues surveyed 6,400 parents of children aged 6 to 14 with the same logic [source: openaccess-livingstone-enabling-2017].

These can show what tends to travel together.

For example, restrictive mediation correlates with fewer reported online risks in the same families.

They cannot show that restriction caused the reduction.

The families who restrict most may also be the families whose children would have had fewer risks anyway.

Specification-curve analyses.

Orben and Przybylski used this approach on three large adolescent datasets totaling 355,358 respondents [source: pubmed-orben-przybylski-2019].

They concluded that digital technology use explains at most 0.4% of the variation in wellbeing.

A specification curve tries every reasonable way of slicing the data — different subsets, different wellbeing measures, different exposure definitions — and reports how robust each finding is.

The 0.4% ceiling is a strong statement.

Average screen time is not a large uniform cause of adolescent wellbeing variation across the populations measured.

Longitudinal cohort studies.

The same participants are followed over time.

The direction of any association can be tested.

Orben and colleagues followed 17,409 participants aged 10 to 21 and reported prospective windows in which higher estimated social-media use predicted lower life satisfaction one year later [source: www-orben-windows-2022].

The windows were 11–13 for females, 14–15 for males, and 19 for both sexes.

Reverse-direction effects — life satisfaction predicting later use — were also observed.

Associations running both ways are common in this literature.

Natural experiments and quasi-experiments.

Braghieri, Levy and Makarin used Facebook’s staggered rollout across US colleges as a generalized difference-in-differences natural experiment [source: www-braghieri-aer-2022] [source: alexeymakarin-braghieri-author-chapter-2023].

They reported poorer student mental-health outcomes after access, with an effect of 0.085 standard deviations on an index of poor mental health.

This is the closest design the field has to a causal estimate of a real platform’s effect on a real population.

It is also a specific population — US college students in the mid-2000s, during Facebook’s early spread.

Its external validity to today’s 13- to 16-year-olds using current mobile platforms is weak [source: www-braghieri-aer-2022].

Meta-analyses.

A meta-analysis pools many primary studies and asks what the literature says in aggregate.

Tan and colleagues’ 2025 meta-analysis is the most recent synthesis of digital parenting as a whole [source: doi-tan-digital-parenting-2025].

Chen and Shi’s earlier meta-analysis covered 52 empirical studies with 74,159 participants and 122 independent correlations [source: doi-chen-shi-mediation-2019].

Jeong and colleagues’ meta-analysis of 51 media-literacy interventions reported an overall d = 0.37 across knowledge, critical thinking, attitudes, self-efficacy and behaviour [source: pmc-jeong-media-literacy-2012].

Carpenter and colleagues extended that to 160 interventions covering 1983 to 2023 with overall positive effects, particularly for media-related outcomes [source: academic-carpenter-media-literacy-2025].

Major consensus reviews.

A panel reviews an entire field and issues a statement of what the literature can support.

The US National Academies’ 2024 review of social media and adolescent health concluded that the literature did not support a population-level causal conclusion that social media causes changes in adolescent health [source: www-nasem-social-media-2024].

The review explicitly noted plausible harms, displacement mechanisms and vulnerable subgroups.

A 2026 umbrella review of 72 reviews — drawing on 17 meta-analyses with 1,070 effect estimates from 452 primary studies for power analyses — found general social-media use only weakly and inconsistently related to wellbeing [source: acamh-tolboell-umbrella-2026].

Problematic social-media use was more consistently associated with ill-being.

Haidt’s 2026 World Happiness Report chapter takes a stronger position, arguing that the accumulated evidence now supports severe direct harms and population-relevant indirect effects [source: www-haidt-whr-2026].

The disagreement between these reviews is partly about evidence weighting.

It is also about exposure definition.

Aggregate “screen time” versus platform-specific mechanisms, population averages versus vulnerable subgroups, cross-sectional associations versus quasi-experiments and time trends: these are not the same evidence.

Both positions should be reported, not picked.

Where technical controls help

Technical controls do specific things.

The evidence supports them in specific places.

For young children, time and content limits are the most defensible part of the toolkit.

Multiple guideline bodies recommend low or no exposure for under-5s [source: who-under5-2019] [source: publications-aap-digital-ecosystems-2026].

They base this on the cleaner evidence that screens in this age band displace sleep, physical play and direct caregiver interaction.

WHO recommends no sedentary screen time for infants and 1-year-olds, and at most one hour per day for ages 2 to 4 [source: who-under5-2019].

Australia’s 24-hour movement guidance recommends no sedentary screen time under age 2 and at most one hour per day for ages 2 to 5 [source: www-au-under5-2026].

England’s 2026 government advice for parents of under-5s says to avoid screen time under 2 except shared interactive activity, and to aim for no more than one hour per day at ages 2 to 5 [source: educationhub-uk-parent-advice-under5-2026].

These recommendations are not derived from randomized trials of parental-control software.

They are recommendations about the underlying exposure — how much sedentary screen time a small child should have — and the controls help a parent enforce them.

For immediate, situational hazards, blocking is fast and indisputable.

The technical action of preventing an app from loading, a contact from being added, or a purchase from being completed does not require a research trial to demonstrate.

This is a mechanical function, not a behavioural intervention.

For the research-supported risk–opportunity trade-off, restriction has a measurable association with fewer reported risks.

In the EU Kids Online survey of 25,142 children aged 9 to 16, restrictive mediation correlated with fewer online risks [source: basw-eu-kids-online-mediation-2012].

The same survey, and Livingstone and colleagues’ later eight-country parent survey of 6,400 families with children aged 6 to 14, also showed the cost [source: basw-eu-kids-online-mediation-2012] [source: openaccess-livingstone-enabling-2017].

Restrictive mediation correlated with fewer online opportunities and skills.

The same evidence shows that enabling mediation — explaining, supporting, and gradually handing over — is associated with more opportunities and more risks together [source: openaccess-livingstone-enabling-2017].

That is not a clean trade.

It is the choice a family has to make with the age and temperament of the child in front of them.

Co-use has the largest meta-analytic association with lower negative digital wellbeing among the parenting categories Tan and colleagues compared [source: doi-tan-digital-parenting-2025].

The same caveat applies.

“Co-use” aggregates very different behaviours, from supportive joint engagement to hovering supervision.

For the youngest children, even co-viewing does not substitute for direct caregiver interaction [source: publications-aap-digital-ecosystems-2026].

Where they do not

They do not demonstrate a population-level effect on adolescent wellbeing.

Orben and Przybylski’s specification-curve analysis put the ceiling at 0.4% of wellbeing variation explained by digital technology use [source: pubmed-orben-przybylski-2019].

The 2026 umbrella review found general social-media use only weakly and inconsistently related to wellbeing [source: acamh-tolboell-umbrella-2026].

The National Academies did not support a population-level causal conclusion [source: www-nasem-social-media-2024].

These are not denials that any individual child is harmed.

They are statements about averages across large populations.

A small average effect can hide a large effect for a vulnerable subgroup.

They do not demonstrate that technical monitoring improves the parent-child relationship.

Ghosh and colleagues surveyed 215 US parent-teen dyads with teens aged 13 to 17.

Monitoring-app use was most common among parents who granted the least autonomy [source: doi-ghosh-control-safety-2018].

Monitored teens also had more online victimisation and peer problems.

Greater parental control correlated with more, not fewer, online risks in that survey.

The authors are careful.

The design cannot rule out reverse causation.

Parents may monitor precisely because a teen already faces greater online risk.

The direction of the finding is not consistent with the claim that monitoring apps are relationship-neutral.

A separate content analysis of child-authored parental-control app reviews by Ghosh and colleagues identified recurring objections about privacy, surveillance, trust and overly restrictive control [source: doi-ghosh-safety-surveillance-2018].

That is qualitative evidence — self-selected reviews of dissatisfied users — and not a causal claim.

It is, however, the largest body of child-voiced feedback in the field [source: doi-ghosh-safety-surveillance-2018].

The authors’ framing was that current control apps may undermine trust and harm children’s relationship with their parents.

They do not translate Orben and colleagues’ reported developmental windows into parental-control switch points.

The reported longitudinal windows — 11–13 for females, 14–15 for males, 19 for both — come from one large observational dataset [source: www-orben-windows-2022].

A direct independent replication of the exact boundaries was not established in the research pass this wiki relies on.

Treating these ages as if they were experimentally confirmed cut-points would outrun the evidence.

They do not, on their own, teach self-regulation.

That is not a finding of a single study.

It is the consistent message from the recent syntheses.

The technical action of blocking access does not transfer into the internal capacity to manage it.

AAP’s 2026 technical report explicitly moves beyond a simple two-hour rule [source: publications-aap-digital-ecosystems-2026].

It treats content, context, displacement and caregiver communication as the organising frame.

RCPCH currently formally endorses no screen-time resource at all [source: www-rcpch-screen-resources-2026].

This is in part because the underlying evidence does not support a universal minute threshold.

They do not produce uniform consensus on numeric limits.

WHO’s under-5 guidance, Germany’s AWMF/DGKJ S2k guideline, Australia’s 24-hour movement guidance, England’s 2026 under-5 advice and Switzerland’s federal parent guidance all publish different numeric schedules [source: who-under5-2019] [source: register-awmf-dgkj-2023] [source: www-au-under5-2026] [source: www-au-5-17-2026] [source: educationhub-uk-parent-advice-under5-2026] [source: jugendundmedien-ch-jugend-medien-6-10].

Germany’s age-by-age schedule sets specific numeric limits for each age band [source: register-awmf-dgkj-2023]:

• No active or passive screen use under age 3.
• About 30 minutes on individual days at ages 3–6.
• 30–45 minutes at ages 6–9.
• 45–60 minutes daily at ages 9–12.
• 1–2 hours at ages 12–16.
• About 2 hours at ages 16–18.

It is an S2k guideline.

S2k is a consensus-based document using a representative panel and formal consensus procedures rather than an S3 systematic evidence synthesis [source: register-awmf-dgkj-2023] [source: www-awmf-levels].

That does not mean the German guideline is wrong.

The exact minute thresholds in any national schedule should be read as a professional translation of incomplete evidence into practical preventive guidance.

Not as established biological cut-points.

What consistently helps more

The non-technical practices the literature supports are remarkably consistent across reviews, even when the technical ones are not.

Media-literacy interventions have measurable intervention effects.

Jeong and colleagues’ meta-analysis of 51 interventions reported d = 0.37 overall across knowledge, critical thinking, attitudes, self-efficacy and behaviour [source: pmc-jeong-media-literacy-2012].

Carpenter and colleagues’ updated meta-analysis of 160 interventions from 1983 to 2023 reported positive effects overall [source: academic-carpenter-media-literacy-2025].

Media-related outcomes responded more than behaviour.

The APA’s 2023 advisory on adolescent social media use recommends that social-media use be preceded by training in social-media literacy [source: www-apa-advisory-2023].

The Swiss federal prevention stance treats media competence as central to preventing problematic use [source: www-ch-bag-media-2022] [source: www-ch-bag-online-behavior].

The honest reading: media literacy reliably moves proximal outcomes (knowledge, critical evaluation, attitudes), and the behavioural effects are real but smaller.

It is not proven to replace technical safeguards.

It does not physically block the acute hazard.

It is, however, the intervention class with the cleanest evidence behind it for building the capacity a teen will need once the controls are off the device.

Co-use and positive mediation travel together with the best non-technical outcomes.

Tan and colleagues’ meta-regression found co-use had the largest negative coefficient for negative digital wellbeing among the compared parenting categories [source: doi-tan-digital-parenting-2025].

Positive mediation was next.

The Swiss federal parent platform recommends involving school-age children in rule-setting, not deciding for them [source: jugendundmedien-ch-jugend-medien-6-10].

For adolescents, the same platform emphasises critical and responsible use, privacy awareness and adult interest rather than technical mastery [source: jugendundmedien-ch-jugend-medien-14plus].

The relationship itself — not the controls — is what the child uses once the screen is open.

Janssen and colleagues’ preregistered 100-day diary study followed 479 Dutch adolescents (mean age 15.98) and found that digital communication with parents occurred on 43% of days [source: doi-janssen-100day-2025].

It averaged about 20 minutes when characterised at study level, largely for micro-coordination [source: doi-janssen-100day-2025].

That is not surveillance.

It is the texture of staying connected without surveillance.

The same body of work identifies that transparent connection is not the same mechanism as covert monitoring [source: doi-ghosh-safety-surveillance-2018].

Family conflict is part of what the technical controls get blamed for when the family context is the actual problem.

A developmental mix is what the evidence supports.

Younger children need more adult structure and co-engagement.

School-age children need clear boundaries plus skills.

Adolescents need proportionate, transparent safeguards alongside autonomy and media literacy.

The same synthesis that produced those claims also produces the caution.

The evidence does not establish that more surveillance generally produces better developmental outcomes [source: ADR-0005].

It does not establish that media literacy alone can replace every protective control.

What we do not know

Some of the most important questions in this domain have no answer in the current evidence.

This page should say so directly.

Whether parental-control software causally prevents serious online harm.

Existing studies are largely cross-sectional [source: doi-tan-digital-parenting-2025].

A prospective or randomized comparison measuring actual harm events — not just screen time, not just parent reports, not just app adoption — has not been done at scale.

Whether covert monitoring damages trust more than transparent monitoring.

The child-authored review evidence is qualitative [source: doi-ghosh-safety-surveillance-2018].

Longitudinal and experimental comparisons with preregistered trust and disclosure measures do not exist in the literature this wiki retrieved.

Whether intrusive monitoring causes teens to hide behaviour, or merely co-occurs with already difficult family situations.

The available monitoring studies cannot separate child risk, prior conflict and monitoring changes over time [source: doi-ghosh-control-safety-2018].

What level of monitoring is optimal at primary-school age versus early-teen versus mid-teen years.

Existing studies and meta-analyses aggregate broad ages and heterogeneous strategies.

Age-stratified prospective intervention evidence does not exist in the literature this wiki retrieved [source: doi-tan-digital-parenting-2025].

Whether Orben and colleagues’ reported 11–13 female and 14–15 male sensitivity windows replicate in independent longitudinal datasets.

A direct preregistered replication with comparable age resolution was not located [source: www-orben-windows-2022].

How much of the Orben and Przybylski small average effect reflects crude self-reported exposure measurement.

Self-reported minutes on a phone are a known under-count [source: pubmed-orben-przybylski-2019].

Studies linking objective platform logs to validated mental-health outcomes at individual level are still emerging.

How transferable the Facebook-rollout natural experiment is to today’s children.

The original population was US college students in the mid-2000s [source: www-braghieri-aer-2022].

Current 13- to 16-year-olds use different platforms on different hardware.

Whether media literacy prevents severe online harms, rather than only changing knowledge and attitudes.

The meta-analytic evidence shows stronger proximal than behavioural effects [source: pmc-jeong-media-literacy-2012] [source: academic-carpenter-media-literacy-2025].

Modern RCTs with long follow-up and behavioural endpoints are not the bulk of what exists.

Which children benefit or suffer most from the same amount and type of media.

Individual-level longitudinal designs covering neurodivergence, baseline mental health, socioeconomic status, sex and gender, family relationships and specific media activities are the explicit gap the National Academies flagged [source: www-nasem-social-media-2024].

What the correct unit of exposure actually is.

Total screen time, platform, content, activity, social context, time of day or problematic-use pattern — these are not interchangeable [source: publications-aap-digital-ecosystems-2026] [source: www-nasem-social-media-2024].

The current evidence argues against treating all digital exposure as homogeneous.

How to read studies about screen time

Five habits help a parent read past the headline.

1. Ask which design produced the number.

A cross-sectional association, a longitudinal window, a meta-analytic average and a natural experiment are four different claims with four different strengths.

Headlines flatten them.

2. Read the effect size, not just the direction.

r = -0.05 is a real association that explains almost no variance [source: doi-tan-digital-parenting-2025].

0.085 SD on a poor-mental-health index is a small effect on a specific historical population [source: alexeymakarin-braghieri-author-chapter-2023].

A 0.4% variance ceiling is the headline a specification-curve analysis produces [source: pubmed-orben-przybylski-2019].

d = 0.37 in a media-literacy meta-analysis is a moderate effect across many proximal measures [source: pmc-jeong-media-literacy-2012].

These four numbers look interchangeable in a press release.

They are not.

3. Distinguish correlation from selection.

When monitored teens show more online risk, the same data can mean monitoring is harmful or that parents monitor more when their child is already at higher risk [source: doi-ghosh-control-safety-2018].

The two have different implications for what to do tonight.

4. Notice the population.

A finding from US college students in 2006 is not a finding about a 13-year-old on TikTok in 2026 [source: www-braghieri-aer-2022].

A finding from 25 European countries in 2012 is not a finding about a 9-year-old using Roblox on a school iPad [source: basw-eu-kids-online-mediation-2012].

5. Distinguish “general use” from “problematic use.”

They have different evidence behind them and different implications for what an intervention should target [source: acamh-tolboell-umbrella-2026].

Calling a high-hours child “addicted” from a screen-time total alone outruns the evidence.

The 2026 umbrella review is explicit on the gap between the two.

If a study does not survive these five checks, it is a study to cite carefully, not a study to act on without thinking.

Children speak — a primary-school perspective

The video below is from the UK Safer Internet Centre’s film for parents and carers, showing children from Walker Primary School talking about the controls their parents have set up at home.

The full evidence review above is the scholarly side of the question.

The video is the children’s side of the same question.

Both responses are consistent: setting matters, but the relationship in which the setting is set matters more.

The card embeds through the privacy-enhanced youtube-nocookie.com domain that the site’s Content-Security-Policy allows.

Sources

This page draws on the following sources.

None is a manufacturer claim.

Every cited study or guideline is peer-reviewed scientific research, an institutional consensus or a professional-body statement.

Peer-reviewed and conference research:

• doi-tan-digital-parenting-2025 — Tan et al., 2025 meta-analysis of 88 digital-parenting studies. Primary source for r = -0.05 across 423 effect sizes and the meta-regression comparing co-use, positive and restrictive mediation.
• basw-eu-kids-online-mediation-2012 — EU Kids Online 2012 research report, N = 25,142 children aged 9 to 16 in 25 countries. Primary source for the risk–opportunity trade-off under restrictive mediation.
• openaccess-livingstone-enabling-2017 — Livingstone and colleagues’ eight-country parent survey, N = 6,400, ages 6 to 14. Primary source for the enabling-vs-restrictive contrast.
• doi-chen-shi-mediation-2019 — Chen and Shi, 2019 parental-mediation meta-analysis, 52 studies, N = 74,159.
• doi-ghosh-control-safety-2018 — Ghosh and colleagues’ 2018 survey of 215 US parent-teen dyads aged 13 to 17 on monitoring-app use.
• doi-ghosh-safety-surveillance-2018 — Ghosh and colleagues’ 2018 CHI content analysis of child-authored parental-control app reviews.
• pubmed-orben-przybylski-2019 — Orben and Przybylski’s 2019 specification-curve analysis, three datasets, N = 355,358.
• www-orben-windows-2022 — Orben and colleagues’ 2022 longitudinal study, N = 17,409 ages 10 to 21, on developmental sensitivity windows.
• www-nasem-social-media-2024 — US National Academies 2024 consensus review of social media and adolescent health.
• acamh-tolboell-umbrella-2026 — 2026 umbrella review of 72 reviews; power analyses drawn from 17 meta-analyses and 452 primary studies.
• www-haidt-whr-2026 — Haidt’s 2026 World Happiness Report chapter on adolescent social-media harm.
• www-braghieri-aer-2022 — Braghieri, Levy and Makarin’s Facebook-rollout natural experiment.
• alexeymakarin-braghieri-author-chapter-2023 — Author-produced summary of the Facebook study; 0.085-SD effect size on the poor-mental-health index.
• pmc-jeong-media-literacy-2012 — Jeong and colleagues’ 2012 meta-analysis of 51 media-literacy interventions; d = 0.37.
• academic-carpenter-media-literacy-2025 — Carpenter and colleagues’ 2025 meta-analysis of 160 media-literacy interventions, 1983 to 2023.
• doi-janssen-100day-2025 — Janssen and colleagues’ preregistered 100-day diary study, N = 479 Dutch adolescents, mean age 15.98.

Institutional and professional guidelines:

• who-under5-2019 — WHO 2019 guidelines on physical activity, sedentary behaviour and sleep for children under 5.
• who-5-17-2020 — WHO 2020 guidelines on physical activity and sedentary behaviour for ages 5 to 17.
• publications-aap-digital-ecosystems-2026 — AAP 2026 technical report on digital ecosystems, children and adolescents.
• www-rcpch-screen-resources-2026 — RCPCH current position on screen-time resources.
• register-awmf-dgkj-2023 — German AWMF/DGKJ S2k guideline 027-075 on prevention of dysregulated screen media use.
• www-awmf-levels — AWMF classification methodology; defines S2k as consensus-based.
• www-au-under5-2026 — Australian 24-hour movement recommendations, birth to 5.
• www-au-5-17-2026 — Australian 24-hour movement recommendations, ages 5 to 17.
• www-au-evidence-review-2019 — Underlying evidence review for the Australian 5–17 recommendations.
• educationhub-uk-parent-advice-under5-2026 — England 2026 parent-facing advice for under-5s.
• www-uk-eystag-report-2026 — England Early Years Screen Time Advisory Group independent evidence report.
• consult-uk-call-5-16-2026 — England call for evidence on screen use by children aged 5 to 16.
• digitalstrategy-eu-bikplus — EU Better Internet for Kids strategy.
• www-apa-advisory-2023 — APA 2023 health advisory on social-media use in adolescence.
• jugendundmedien-ch-jugend-medien-6-10 — Swiss federal Jugend und Medien guidance for ages 6 to 10.
• jugendundmedien-ch-jugend-medien-14plus — Swiss federal Jugend und Medien guidance for adolescents aged 14 and up.
• www-ch-bag-media-2022 — Swiss Federal Office of Public Health on media consumption by children and adolescents.
• www-ch-bag-online-behavior — Swiss BAG on problematic online behaviour and the role of media competence.

[source: ADR-0005] — editorial stance on control versus competence, the decision this page is grounded in.