Published on 16 September 2026
Online parent-led CBT to prevent child anxiety: what does a trial in 95 English schools show?
In brief
Ninety-five English schools, screening offered to every family in the sampled classes, and 865 children aged 4 to 7 enrolled because they had at least one risk factor for anxiety. The intervention is delivered neither to the child nor in the school: parents work through seven online modules of cognitive behavioural therapy, each supported by a brief call with an NHS practitioner. Twelve months later, the frequency of anxiety disorders, established by a diagnostic interview conducted blind, is 6.8% (21 of 310) in the intervention arm against 11.5% (36 of 312) in the usual school practice arm, an adjusted odds ratio of 0.67 (95% confidence interval 0.37 to 1.21, p = 0.19). The primary outcome therefore does not reach statistical significance in the intention-to-treat analysis. At the same time, all ten secondary outcomes are significant in favour of the intervention, at twelve weeks (standardised mean differences 0.15 to 0.47) as at twelve months (0.19 to 0.41). The diagnostic interview could be obtained for only 72% of children, which weakens interpretation in both directions.
The context
Anxiety in school-age children is common, poorly recognised and treated late. In the consulting room it rarely presents under that name: it is Sunday-evening stomach aches, an emerging school refusal, a child described as shy. Universal prevention programmes, that is programmes offered to every child in a class and not only to children who have been identified, are an appealing public health response, but their real effectiveness remains debated. The strategy assessed here is different: screening is universal, the intervention is not. All families in the participating classes received the questionnaires, and only children who screened positive on at least one of the three best-established risks, child anxiety symptoms, behavioural inhibition, parental anxiety, entered the trial.
The originality of the set-up lies in two choices. First, it is not addressed to the child: the parents follow the programme, which is the rule under the age of eight, for want of validated self-report tools at that age. Second, it requires neither travel nor group sessions: parents work on an online platform, each module being supported by a short call with a practitioner trained in low-intensity therapies. The school is only the place where children are identified. The wager is twofold: to act on parental responses to avoidance, and to do so with an amount of therapist time compatible with deployment across a whole area, here 152 minutes per family on average.
The study at a glance
| Item | |
|---|---|
| Population | |
| Detail865 children aged 4 to 7 (Reception, Year 1, Year 2), attending 95 mainstream primary schools in England. Of 15,447 families invited, 2,328 children were screened (15%), 1,172 were eligible (50% of those screened) and 865 were enrolled (74% of those eligible). Eligibility: at least one positive score among a preschool anxiety scale score of 34 or more out of 112, an inhibition subscale score of 30 or more out of 42, or a parental GAD-7 score of 8 or more out of 21. No diagnosis was required and none was excluded. One child per family. Two further conditions: sufficient command of English and regular internet access. | |
| Intervention | |
| DetailOSI (Online Support and Intervention for child anxiety), parent-led cognitive behavioural therapy: seven online modules, each accompanied by a brief weekly telephone or video call, then a follow-up call about four weeks after the final content. An optional game app for the child is offered. The therapists were five Children’s Wellbeing Practitioners from the NHS, low-intensity practitioners trained over one year, supervised every week by a clinical psychologist. 434 children, of whom 332 (76%) completed the core content and 73% the full programme. Mean therapist time: 152 minutes per family. | |
| Comparator | |
| DetailUsual school practice, 431 children. Schools in both arms kept their full usual provision and families in both arms remained free to seek any care. Schools’ social and emotional provision was measured with a dedicated questionnaire (mean score 8.25 out of 30) and did not differ between arms. After the twelve-month assessment, families in the control arm received the programme content in text and audio versions. | |
| Primary outcome | |
| DetailPresence or absence of an anxiety disorder at twelve months, established with the ADIS-P, a semi-structured diagnostic interview conducted with the parent and adapted to DSM-5 criteria. A diagnosis was retained only with a clinical severity rating of 4 to 8. Interviews were conducted by assessors blind to trial arm, and the final diagnosis was agreed in a meeting led by an experienced diagnostician who was also blind. Systematic double rating: kappa 0.85 for diagnosis, intraclass correlation coefficient 0.91 for severity. | |
| Secondary outcomes | |
| DetailTen questionnaires, all completed by the parent, at twelve weeks and twelve months. Three risk factors: child anxiety symptoms, behavioural inhibition, parental anxiety. Two broader clinical outcomes: interference of anxiety with the life of the child and family, externalising symptoms. Five direct intervention targets: parental overprotection, parental self-efficacy, child behavioural avoidance, intolerance of uncertainty, perceived efficacy of coping strategies. | |
| Design | |
| DetailPragmatic, parallel-group, superiority cluster randomised trial, the unit of randomisation being the school. 1:1 allocation in blocks of two and four, stratified by school-level deprivation (above or below the national median of 15.8% of pupils eligible for free school meals), carried out by an independent statistician after baseline data collection. Primary intention-to-treat analysis on fifty imputed data sets: generalised estimating equations for the binary outcome, mixed models for the continuous outcomes, in both cases accounting for within-school correlation. Prospective registration ISRCTN82398107 on 14 January 2021, protocol and statistical analysis plan published before analysis. |
Quality control
| Criterion | Status |
|---|---|
| Unit of randomisation and analysis | Consistent |
| FindingRandomisation is by school and the analysis accounts for within-school correlation. That is the condition for validity in a cluster trial, and it is met. Clustering turned out to be much weaker than expected: the adjusted intra-cluster correlation coefficient for the primary outcome is 0.009, against the 0.05 assumed in the sample size calculation. | |
| Pre-specified primary outcome | Yes, assessed blind |
| FindingThe primary outcome is a diagnosis established by interview with blinded assessors, not a scale completed by the trained parent. Thirteen per cent of participants (81 of 622) revealed their arm during the interview, but the supervisor remained blind until diagnostic agreement. This choice protects against most reporting bias. | |
| Loss to follow-up | 28% on the primary outcome |
| Finding622 children out of 865 had the diagnostic interview at twelve months, a retention of 72%, below the 80% target used in the sample size calculation. 78% provided at least one outcome at twelve months. This is the main limitation of the trial, and it explains the gap between the two analyses presented below. | |
| Blinding | Not possible for parents |
| FindingA parent knows whether they followed the programme, and the team members in contact with schools and families knew too. All ten secondary outcomes, completed by that same parent, are affected, which gives the primary outcome, assessed blind, a particular weight. | |
| Funding | Non-industry |
| FindingThe trial is funded by the health research programme of a private not-for-profit foundation, the Kavli Trust. The funder had no role in study design, data collection, analysis or interpretation, or in writing. Several authors also receive individual public or charitable support, which does not concern the trial itself. | |
| Competing interests | Royalties on the platform |
| FindingTwo authors, including the last author, developed the platform under evaluation. No remuneration was received for its use during the study, but one of them may receive personal royalties from wider implementation, and the University of Oxford will receive royalties and consultancy fees for the contribution of the other, who receives nothing personally. On top of a classic allegiance bias, whose documented effect in psychotherapy bears mainly on unblinded outcomes, there are therefore downstream financial interests declared by the authors. | |
The findings
| Outcome | Result |
|---|---|
| Frequency of an anxiety disorder at twelve months | 6.8% (21 of 310) against 11.5% (36 of 312) |
| PEB readingThe absolute difference is 4.7 points. The main reason the primary outcome failed is not clustering by school, whose measured effect is negligible, but the observed frequency: the trial was powered to detect a fall from 50% to 35%, an assumption drawn from an earlier trial in children selected on inhibition alone. It ended up comparing 11.5% with 6.8%. The authors say so themselves: detecting the same relative reduction at this level of frequency would have required a much larger sample. | |
| Intention-to-treat analysis, multiple imputation | Adjusted odds ratio 0.67 (0.37 to 1.21), p = 0.19 |
| PEB readingThis is the primary analysis, the one that answers the question asked. It is negative in the strict sense of the word, which does not mean that it demonstrates an absence of effect. | |
| Complete case analysis | Adjusted odds ratio 0.57 (0.34 to 0.96), p = 0.034 |
| PEB readingThis analysis covers only the families followed to the end. The authors explicitly judge it less robust than the primary analysis, and that is the right call: the families lost to follow-up differ from the others, as is known with certainty here. A result of this kind suggests, it does not demonstrate. | |
| Sensitivity analyses | Same direction, same conclusion |
| PEB readingThe complier average causal effect analysis gives 0.54 (0.24 to 1.27) on imputed data and 0.53 (0.26 to 0.84) on complete cases. The analysis restricted to interviews carried out within the planned data collection window gives 0.65 (0.36 to 1.17), p = 0.15 on imputed data and 0.54 (0.32 to 0.90), p = 0.018 on complete cases. The pattern repeats: as soon as data are imputed, the interval crosses 1; as soon as the analysis is restricted to responders, it no longer does. | |
| Secondary outcomes | Ten out of ten significant, effects 0.15 to 0.47 at twelve weeks and 0.19 to 0.41 at twelve months |
| PEB readingThe largest effects concern parental overprotection (0.47 at twelve weeks, 0.41 at twelve months) and child anxiety symptoms (0.43 then 0.35). The smallest concern externalising symptoms (0.15 at twelve weeks) and inhibition (0.19 at twelve months). Unlike the primary outcome, these results are consistent between imputed data and complete cases. The convergence is therefore statistically solid. It remains the least protected part of the design, since all ten measures come from a single informant who knows what they received. | |
| Safety | No serious adverse events |
| PEB readingOne adverse event related to trial procedures in each arm. Five participants, four of them in the control arm, reported expected discomfort related to completing the questionnaires, and four participants in the intervention arm reported mild discomfort related to taking part in the programme. Nothing that weighs against the benefit-risk balance of an intervention of this kind. | |
A number needed to treat is not reported by the authors, and it cannot be calculated here. It would require an estimated risk difference with its confidence interval; yet the primary analysis is inconclusive, and the observed difference in frequencies concerns only the children actually assessed, that is a population known not to be representative of all those enrolled.
Critical appraisal
| Domain | Judgement |
|---|---|
| Randomisation process | Low risk |
| FindingAllocation in blocks of two and four, stratified by school-level deprivation, carried out by a statistician independent of the trial after baseline data collection, with schools ordered by size to limit imbalance between arms. School and participant characteristics are comparable between arms, except for the last recruitment cohort (40 children against 12), an imbalance handled by adjusting for cohort. No school left the trial. | |
| Deviations from protocol | Reservation |
| FindingAn open trial by nature. Adherence is good for this type of format: 76% of families in the intervention arm completed the core content and 73% the full content, compared with the 34% attendance at group sessions and the 25% completion of an unsupported online programme reported in earlier trials. The complier average causal effect analysis does not change the conclusion on the primary outcome. | |
| Missing data | High risk |
| FindingTwenty-eight per cent of children without a diagnostic interview at twelve months. Rates are comparable between arms, but the children without diagnostic data more often came from disadvantaged backgrounds and single-parent households, and had poorer clinical functioning at baseline. In other words, the data are not missing completely at random. Multiple imputation corrects under the assumption that they are missing at random conditional on the variables in the model, an assumption that cannot be verified. The gap between the two analyses is precisely the measure of that uncertainty. | |
| Measurement of the outcome | Low risk |
| FindingThe reference semi-structured diagnostic interview in the field, assessors and supervising diagnostician blind, double rating of all interviews, high inter-rater agreement. The contrast is sharp with the secondary outcomes, which all rest on a single unblinded informant. | |
| Selection of the reported result | Low risk |
| FindingProspective registration, protocol and statistical analysis plan published before analysis, statisticians blind until database lock. The negative primary result is reported as such and the conclusion does not substitute a secondary outcome for it. That is what sets this trial apart from many others. | |
| External validity | Selection at entry |
| FindingOnly fifteen per cent of invited families responded to screening, against the 50% expected, and half of the children screened turned out to be eligible, which signals self-selection by the families concerned. The most deprived schools screened and enrolled markedly fewer children (18 screened and 7 enrolled on average, against 30 and 11 elsewhere), and families in rented housing, with lower education, unemployed, single-parent or from minoritised ethnic backgrounds were under-represented among those enrolled. Eighty-seven per cent of children and 90% of parents were described as White, against 82% of the population of England and Wales. Two eligibility conditions also exclude part of the target population: command of English and regular internet access. A single country, a single school system, and a profession, the Children’s Wellbeing Practitioner, defined within the NHS, whose transfer to other health systems the publication does not examine. | |
Level of evidence
Confidence is high on the experimental side: a cluster randomised trial of this size, prospectively registered, with a published protocol and analysis plan, a diagnostic primary outcome assessed blind and a correctly adjusted analysis, is the most solid thing the prevention literature produces. It is also high on the honesty of the report, since the negative primary result is owned all the way to the conclusion.
Three levels then need to be distinguished. What is demonstrated is that the programme improves what parents measure: ten outcomes out of ten, at two time points, with results consistent between the imputed analysis and the complete case analysis, which is rare and counts. What is not demonstrated is a reduction in diagnosed anxiety disorders at twelve months: the primary analysis is inconclusive, and the only significant result on this outcome comes from an analysis restricted to families followed to the end, that is from the very mechanism by which selection bias produces an apparent effect. What remains open is two things: the share of the effects on secondary outcomes attributable to a single unblinded informant, and whether these effects eventually translate into fewer established disorders in the longer term, which the trial did not measure. On this last point precision matters: this is not an absence of signal, it is an absence of analysis. Follow-up stops at twelve months.
One final element deserves to be stated, because it weighs more than anything else on the interpretation of the primary outcome. The trial was built on the assumption that half the children in the control arm would have an anxiety disorder at twelve months. The figure was 11.5%. The gap between assumption and observation does not reflect a flaw in conduct, but the fact that screening for three risks in the general school population does not select the same population as selecting inhibited children in the laboratory. The consequence is mechanical: the real power of the trial on this outcome was far lower than planned.
The colleague test
What an experienced colleague would say if you put this study to them in two minutes, between two consultations.
“ A clean trial, in 95 schools, that misses its primary outcome and wins on the other ten. The problem is not the conduct, it is that it was powered on an expected prevalence of 50% and observed 11.5%. What I take away is that online parent-led CBT, with two and a half hours of therapist time per family, shifts everything the parents measure, and that three families out of four see it through. What I do not take away is that it prevents anxiety disorders. ”
What this means in practice: the value of this trial is not to supply a programme to recommend, since the publication does not document its availability outside the trial setting, but to show that a light, remote format supported by brief calls holds up in ordinary families and produces a measurable signal where little was expected. It is an argument for referring to existing parent guidance, not for promising that it prevents disorders.
What you can do with this
- Faced with a child aged 4 to 7 described as anxious, the useful person to talk to is the parent. What this trial makes defensible is spending time on the parent’s response to avoidance behaviours, and in particular on overprotection, which is here the target with the clearest effect, without waiting for an established disorder to justify individual treatment.
- To a parent who asks whether a brief programme is any use, the honest answer is that the effects on symptoms and on parenting behaviours are real and reproduced from one analysis to the next, but that the best-conducted trial did not show a reduction in diagnosed anxiety disorders. It is a reason to try, not a promise.
- The format matters as much as the content: seven online modules, short weekly calls, about two and a half hours of therapist time per family, and three families out of four who complete it, where in-person group sessions retained only one in three. What limits the reach of parent guidance in practice is rarely its content, it is its accessibility.
- Parental anxiety is here one of the three entry criteria, and it improves with the intervention. A useful reminder: asking about the parent’s anxiety when faced with an anxious child is not a digression, it is part of the assessment.
- This trial is a good teaching case for explaining, to a trainee or a colleague, why a complete case result does not replace an intention-to-treat analysis, and why an overestimated prevalence assumption can doom a trial before it even starts.
- What remains to be watched: whether the benefit persists beyond twelve months, which was not measured here.
- The course of action is set out in the NICE decision tree for generalised anxiety and panic disorder.
Frequently asked questions
Is this trial of online parent-led CBT for child anxiety positive or negative?
Negative on what it committed to measuring, positive and significantly so on the ten secondary outcomes. Both statements are true at the same time, and presenting them separately amounts to choosing one’s conclusion in advance.
Why not rely on the complete case analysis, which was significant?
Because it excludes the families lost to follow-up, a little under three in ten. Here it is known that these families differ from the others: they were more often disadvantaged and single-parent, and their children were doing less well at baseline. The complete case result is therefore biased, in a direction that is not known with certainty but that is anything but random. The intention-to-treat analysis exists for this reason, and the authors themselves favour it.
Is a standardised mean difference of 0.15 to 0.47 clinically meaningful?
These children are not drawn at random: all of them have at least one risk factor identified at screening. In such a population, an effect of this size moves each child moderately, but it bears on targets known to predict future anxiety, parental overprotection first among them. That is the reasoning of targeted prevention, and it does not carry over as it stands to the patient who presents with an established disorder.
Does it matter that some of the authors developed the programme?
It disqualifies nothing, and the links are declared precisely, including possible future royalties. But it weighs mainly on the outcomes that parents complete themselves. It is one more argument for giving the primary outcome, assessed blind, the place it holds here.
Can this online parent-led programme be used in routine practice?
Not as it stands. It rests on a dedicated platform and on a profession, the Children’s Wellbeing Practitioner, defined within the NHS, and the publication does not document the availability of the programme outside the trial setting, nor does it examine its transfer to other health systems. It also assumes regular internet access and command of the language, two conditions required at enrolment. And the most uncomfortable figure in the trial should be kept in mind: 15% of invited families responded to screening. What can be transferred is the principle of brief, remote, supported parent guidance, not the set-up itself.
Annotated bibliography
Source study. Reardon T, Ukoumunne OC, Dodd H, Halliday G, Hill C, Jasper B, Jones B, Lawrence PJ, Morgan F, Placzek A, Rapee RM, Violato M, Yu S, MYCATS Team, Creswell C. Parent-led CBT delivered via online and telephone support alongside usual school practice versus usual school practice only for young children identified as at risk for anxiety disorders through screening in schools: a cluster randomised controlled trial. Journal of Child Psychology and Psychiatry. 2026; 67(8): 1280-1296. DOI 10.1111/jcpp.70119 · PMID 41711297. Funding: Kavli Trust Programme on Health Research, the funder having had no role in design, data collection, analysis, interpretation or writing; individual support for authors from the NIHR, UKRI (fellowship MR/S017909/1) and the Prudence Trust. Competing interests: C. Creswell and C. Hill developed the platform under evaluation, without remuneration during the study; C. Hill may receive personal royalties from wider implementation, and the University of Oxford will receive royalties and consultancy fees for the contribution of C. Creswell, who receives no personal income; the other authors declare no competing interests.
Protocol registration. ISRCTN82398107, prospectively registered on 14 January 2021. Protocol and statistical analysis plan published before analysis. Ethical approval: University of Oxford Medical Sciences Interdivisional Research Ethics Committee, reference R62531, dated 6 January 2021.