Nurse-delivered sleep restriction therapy to improve insomnia disorder in primary care: the HABIT RCT

Article history

The research reported in this issue of the journal was funded by the HTA programme as award number 16/84/01. The contractual start date was in October 2017. The draft manuscript began editorial review in September 2021 and was accepted for publication in May 2022. The authors have been wholly responsible for all data collection, analysis and interpretation, and for writing up their work. The HTA editors and publisher have tried to ensure the accuracy of the authors’ manuscript and would like to thank the reviewers for their constructive comments on the draft document. However, they do not accept liability for damages or losses arising from material published in this article.

Copyright statement

Copyright © 2024 Kyle et al. This work was produced by Kyle et al. under the terms of a commissioning contract issued by the Secretary of State for Health and Social Care. This is an Open Access publication distributed under the terms of the Creative Commons Attribution CC BY 4.0 licence, which permits unrestricted use, distribution, reproduction and adaption in any medium and for any purpose provided that it is properly attributed. See: https://creativecommons.org/licenses/by/4.0/. For attribution the title, original author(s), the publication source – NIHR Journals Library, and the DOI of the publication must be cited.

2024 Kyle et al.

Objectives

The primary objective of the Health-professional Administered Brief Insomnia Therapy (HABIT) trial was to establish whether nurse-delivered SRT for insomnia disorder in primary care improves insomnia more than SH. We hypothesised that participants allocated to SRT would demonstrate lower insomnia severity at 6 months post randomisation compared with those allocated to SH.

Our secondary hypotheses were as follows:

1. Compared with SH, participants allocated to SRT would report improvements in health-related quality of life (HRQoL), sleep-related quality of life, depressive symptoms, work productivity, pre-sleep arousal and sleep effort (at 3, 6, and 12 months).

2. Compared with SH, participants allocated to SRT would demonstrate improvements in sleep parameters (diary and actigraphy-recorded) and report a reduction in use of sleep-promoting medication (6 and 12 months).

3. The effect of SRT on insomnia severity would be mediated via reduction in sleep effort and pre-sleep arousal.

Other objectives:

1. To establish whether nurse-delivered SRT for insomnia disorder in primary care is cost-effective compared with SH, from a NHS Personal Social Services (PSS) perspective, and from a societal perspective.

2. To undertake a process evaluation to understand intervention delivery, fidelity and acceptability.

3. To test whether insomnia phenotype moderates clinical benefit obtained from SRT. One prominent model posits that participants with objective short sleep duration are less likely to experience improvement in insomnia relative to those with normal sleep duration. 5 We will examine whether actigraphy-defined sleep duration (< 6 vs. ≥ 6 hours) at baseline moderates the effect of SRT on clinical outcomes (at 6 months).

4. To test whether SRT adherence is associated with degree of clinical change (ISI) from baseline to 3 months, and from baseline to 6 months.

Study design

The HABIT trial was a pragmatic, multicentre, individually randomised, parallel-group, superiority trial. Participants were recruited from general practices across three regions in the UK (Thames Valley, Greater Manchester and Lincolnshire). Assessments took place at baseline and 3, 6 and 12 months post randomisation. The trial was prospectively registered with the ISRCTN (ISRCTN42499563).

Practice and participant recruitment

We identified interested practices in three regions of England (Thames Valley, Greater Manchester and Lincolnshire) through local clinical research networks (LCRNs). In collaboration with the lead CRN, we devised search criteria to identify potentially eligible individuals from practice records. Since insomnia is not commonly coded within practices, records were initially searched for broad sleep-related terms (e.g. cannot sleep, insomnia, non-organic sleep disorders), sleep-related medications (e.g. hypnotics, sedative antidepressants), and key conditions characterised by insomnia (e.g. depressive disorder, fatigue), while applying exclusion criteria (e.g. pregnancy, age, dementia). While this meant that we identified and invited a large number of participants per practice (see Appendix 1), it did increase the possibility of reaching a varied group of people with insomnia. Searches were performed by practice managers, and GPs were given the opportunity to review the list prior to study invitation. Practice managers mailed invitations to identified individuals using Docmail. We also identified potential participants through (1) direct face-to-face GP referral (participants were provided with an information sheet and contact details for the research team), (2) placing posters in practices (containing study contact details) and (3) posting study adverts on practice websites.

Alongside the study invitation letter and participant information sheet, participants were provided with three potential methods to engage with the eligibility process, depending on preference: (1) web-link to complete an online eligibility questionnaire, (2) a brief paper questionnaire with return reply slip (following which the research team contacted participants by phone to complete the remainder of the screening process) and (3) contact details for the research team to arrange completion of the eligibility questionnaire over the phone. Regardless of methods, all interested participants underwent the same eligibility screening questionnaire.

Eligibility criteria

The inclusion criteria were as follows: (1) participant is willing and able to give informed consent for participation, (2) screens positive for insomnia symptoms on the Sleep Condition Indicator34 and meets Diagnostic and Statistical Manual of Mental Disorders, Fifth Edition35 (DSM-V) criteria for insomnia disorder, (3) self-reported sleep efficiency (SE) < 85% over the past month,36 (4) age ≥ 18 years and (5) able to attend appointments during baseline and 4-week intervention (both face-to-face at the practice and over the phone) and adhere to study procedures.

Exclusions were limited to conditions which may be contraindicated for SRT, or render SRT inappropriate or ineffective: (1) pregnant/pregnancy planning in the next 6 months; (2) additional sleep disorder diagnosis (e.g. restless legs syndrome, obstructive sleep apnoea, narcolepsy) or ‘positive’ screen on screening questionnaire;37 (3) dementia or mild cognitive impairment (MCI); (4) diagnosis of epilepsy, schizophrenia or bipolar disorder; (5) current suicidal ideation with intent or attempted suicide within past 2 months; (6) currently receiving cancer treatment or planned major surgery during treatment phase; (7) night, evening, early morning or rotating shift-work; (8) currently receiving psychological treatment for insomnia from a health professional or taking part in an online treatment programme for insomnia; (9) life expectancy of < 2 years; and (10) another person in the household already participates in this trial.

On completion of screening, eligible participants were invited to a baseline appointment with a member of the research team where they provided written informed consent, completed baseline questionnaires, and were provided with a sleep diary and actigraph watch for the following week. Participants subsequently returned the completed diary and actigraph watch to the research team via postal mail, and were then randomised.

Interventions

Outcomes

A list of outcomes and time points and corresponding objectives can be found in Table 2.

Measures

Insomnia severity. Insomnia severity was measured with the ISI,40 a validated self-report questionnaire, at baseline and 3, 6 and 12 months post randomisation. The ISI is a seven-item self-report measure assessing both night-time and day-time symptoms of insomnia. The possible range on the scale is from 0 to 28, with higher scores indexing more severe insomnia symptoms. The internal consistency of the measure is high (α > 0.90) in both clinical and community samples. 41 An ISI score of ≥ 11 is sensitive for insomnia disorder while a ≥ 8-point reduction is associated with moderate improvement in insomnia as assessed by an independent rater. 41

Health-related quality of life. HRQoL was assessed with the Short Form questionnaire-36 items (SF-36)42 [mental component summary (MCS) score and physical component summary (PCS) score] at baseline and 3, 6 and 12 months post randomisation.

Sleep-related quality of life. Sleep-related quality of life was measured with the Glasgow Sleep Impact Index3 (GSII, ranks 1–3) at baseline and 3, 6 and 12 months post randomisation. At baseline, the GSII asks participants to generate, in their own words, three areas of sleep-related impairment. These areas are ranked in order of concern (1–3) and then rated on a visual analogue scale with respect to the previous 2 weeks (0–100, with lower scores indicating greater level of impairment). At follow-up, participants are asked to rate the same areas of impairment, enabling group-level analyses on the three patient-generated ranks.

Depressive symptoms. Depressive symptoms were assessed with the Patient Health Questionnaire-943 (PHQ-9) at baseline and 3, 6 and 12 months post randomisation.

Work productivity. Work productivity was assessed with the self-rated productivity and activity impairment questionnaire44 (WPAI) at baseline and 3, 6 and 12 months post randomisation. The WPAI yields three outcomes for those engaged in employment: absenteeism (% work time missed due to insomnia), presenteeism (% impairment while working due to insomnia) and work productivity loss (overall work impairment/absenteeism plus presenteeism due to insomnia). The final outcome relates to non-work activity impairment and can be completed by all participants.

Pre-sleep arousal. Pre-sleep arousal was measured with the pre-sleep arousal scale45 (PSAS) at baseline and 3, 6 and 12 months post randomisation.

Sleep effort. Sleep effort was assessed with the Glasgow Sleep Effort Scale46 (GSES) at baseline and 3, 6 and 12 months post randomisation.

Sleep parameters. Self-reported sleep parameters were derived from sleep diaries. Participants completed the consensus sleep diary47 for 7 days at baseline and 6 and 12 months post randomisation. Objective sleep-parameters were obtained from actigraphy. Participants wore an actigraph watch (MotionWatch 8, CamNtech Ltd., Cambridge, UK) for 7 days at baseline and 6 and 12 months post randomisationand were instructed to press a marker button on the watch when attempting sleep. These event markers were used to define sleep periods by an experienced scorer blinded to treatment allocation. In the absence of event markers, a decision was made based on bed and rise times from the sleep diary following a decision flow-chart developed at the Sleep and Circadian Neuroscience Institute, University of Oxford. Sleep variables of interest were calculated by the validated in-built algorithm of the MotionWare software 1.2.47. The following sleep parameters were derived from sleep diaries and actigraphy recordings: sleep onset latency (SOL), wake-time after sleep onset (WASO), SE, sleep quality (SQ, diary only) and TST.

Sleep-promoting medication. Medication use was quantified from sleep diaries at baseline and 6 and 12 months post randomisation. Use of prescribed hypnotics and other sleep-promoting medications (e.g. sedative antidepressants, antihistamines, antipsychotics, melatonin) was extracted in order to capture (1) proportion of nights of use per participant and (2) proportion of participants in each group at each time point who used sleep promoting medication at least once during the 7-day recording period.

Cost-effectiveness. Intervention records captured the number and duration of nurse-led sessions to quantify cost of delivery per trial participant. The Client Service Receipt Inventory48 (CSRI) captured self-reported service use, the WPAI was used to index productivity losses and utilities were measured with the EuroQol Questionnaire49 [EuroQol-5 Dimensions, three-level version (EQ-5D-3L)] to enable calculation of quality-adjusted life-years (QALYs). In addition to the EQ-5D-3L, participants completed two additional utility measures, the Short-Form-6 Dimensions (SF-6D)50 (derived from the SF-36) and the EQ-5D-3L + Sleep,51 at 3, 6 and 12 months. EQ-5D-3L + Sleep contains the same five dimensions as the original EQ-5D-3L questionnaire plus an extra dimension on sleep. A value set has been developed for EQ-5D-3L + Sleep enabling utility values to be obtained. 51 Utility values derived from the SF-6D and EQ-5D-3L + Sleep were used to estimate QALYs over the 12-month trial period so that we could assess, in pre-defined exploratory analyses, whether sensitivity to SRT could be improved with these measures (relative to the standard EQ-5D-3L).

Process evaluation. Semistructured interviews were conducted with trial participants, nurses, GPs or practice managers across the three study sites and throughout the trial. Number of appointments attended/received by participants, fidelity appraisal of recorded consultations, and adherence to the prescribed sleep window were also considered. Fidelity of sessions was assessed by a clinical psychologist for a subsample of recordings using a bespoke rating scale (range 0–26 for treatment session 1 and 0–16 for session 3) and converted to % score. Adherence to the prescribed sleep window (intervention group only) was quantified as the number of nights per week that the participant adhered (within 15 minutes) to the nurse-prescribed bed and rise times. Bed and rise times were derived from sleep diaries completed during the 4-week intervention phase and converted to a % score. Adherence was computed for participants with a minimum of 14 out of 28 diary days. Control group contamination (i.e. the possibility that participants in the SH arm access SRT via the trained PN) was assessed using an item from the CSRI and positive responses were followed up via phone interview to collect further information.

Serious adverse events (SAEs). We defined SAEs as any untoward medical occurrence that (1) results in death, (2) is life-threatening, (3) requires inpatient hospitalisation or prolongation of existing hospitalisation, (4) results in persistent or significant disability/incapacity or (5) consists of a congenital anomaly or birth defect. Nurse therapists and participants were prompted to self-report SAEs. Along with self-reporting of SAEs, we also used responses on the CSRI which includes questions on hospitalisations, to follow up participants who reported being hospitalised. We recorded planned hospital admissions at baseline and, when they occurred, these were not counted as SAEs. SAEs were assessed for severity, seriousness and relatedness to study procedures by a medically qualified member of the team. SAEs are reported after date of randomisation until either the date of trial withdrawal or 6-month follow-up completion, whichever was earlier.

Adverse events (AEs). We recorded incidences of falls, accidents (including road-traffic accidents and work-related injuries), near-miss driving incidents, and falling asleep while driving alongside outcomes at baseline and 3, 6 and 12 months post randomisation.

Sample size

It was estimated that 235 participants would be required in each group to detect a group difference of 1.35 points [standard deviation (SD) = 4.5] on the ISI with a power of 90% at 5% level of significance (two-sided). This equates to a standardised effect size of 0.3. The SD was chosen based on the results from the primary care evaluation of SRT. 28 Accounting for 20% attrition we aimed to recruit 588 participants (294 per group). During the trial, overall attrition initially appeared higher than expected, and therefore we made a protocol amendment to increase the sample size depending upon attrition. Research Ethics Committee (REC) approval for the change was obtained in February 2020. We sought a sample size of 628 participants if attrition was 25% or less, and 672 participants if it was between 25% and 30%. Attrition was estimated to be around 25% and therefore our revised target sample size was 628.

For the process evaluation interviews, we aimed to recruit up to 15 participants from each of the 3 stakeholder groups (trial participants, nurses, GPs or practice managers), consistent with our previous experience of framework analysis52 and ensuring a sufficient number of interviews to achieve theoretical data saturation. 53

Randomisation

Participants who completed baseline assessments (including having completed at least 4 days of sleep diary) were eligible for randomisation. Participants were randomised (1 : 1) to SRT or SH using a validated web-based randomisation programme (Sortition), with a non-deterministic minimisation algorithm to ensure site, use of prescribed sleep-promoting medication (yes/no), age (18–65 vs. > 65 years), sex, baseline insomnia severity (ISI score < 22 vs. 22–28) and depression symptom severity (PHQ-9 score < 10 vs. 10–27) were balanced across the two groups. Appropriate study members at each site had access to the web-based randomisation software to complete randomisation and subsequently informed participants of their allocation.

Blinding

This was an open-label study and therefore both participants and nurses were aware of allocation. The participant information sheet informed participants that the study compared two different sleep intervention programmes but did not reveal the study hypothesis. Treatment providers (nurses) were not involved in the collection of trial outcomes. Outcomes (questionnaires, diaries and actigraphy) were self-completed, remotely, by participants. Due to impracticalities associated with blinding of the research team, combined with minimal risk of bias due to use of self-report outcome measures, researchers at each site were aware of treatment allocation. Communication from the research team to participants, post randomisation, was limited to collection of outcome assessments and not therapeutic procedures. The statisticians remained blind to allocation. A full detailed statistical analysis plan (SAP) was prepared and finalised before data collection was complete.

Statistical methods

Descriptive statistics of recruitment, dropout and completeness of interventions were calculated. Baseline variables are presented by randomised group using frequencies (with percentages) for binary and categorical variables, and means (and SDs) or medians (with lower and upper quartiles) for continuous variables. There were no tests of statistical significance nor confidence intervals for differences between groups on any baseline variables. There was no planned interim analysis for efficacy or futility.

The primary analysis population included all eligible randomised participants who had at least one outcome measurement. Participants who withdrew from the trial were included in the analysis until the point at which they withdrew. Participants were analysed according to their allocated treatment group irrespective of what treatment they actually received. Every effort was made to follow up all participants.

Primary outcome. A three-level linear mixed-effect model was fitted to the ISI score assessed at 3, 6 and 12 months following randomisation. Practice and participant were included as random effects. The model specified an unstructured variance–covariance structure for the random effects. Fixed effects included randomised group, minimisation factors [baseline ISI score (continuous), site, age (continuous), use of prescribed sleep promoting medication (yes/no), sex and baseline PHQ-9 score (continuous)], time, and a time by randomised group interaction term to allow estimation of treatment effect at each time point. The estimated difference between arms at 6 months was extracted from the model by means of a linear contrast statement.

Secondary outcomes. Continuous secondary outcomes were analysed using the same method. Secondary outcomes that were binary were analysed using generalised linear mixed-effect models with appropriate link function. For continuous outcomes standardised effect sizes (Cohen’s d) were calculated as the adjusted treatment effect divided by the pooled SD at baseline.

The Mann–Whitney test was used for three of the secondary outcomes (WPAI absenteeism, proportion of days usage of prescribed hypnotic medication, and proportion of days usage of prescribed other medication) due to violation of model assumptions. The p-value for a difference is reported at each time point, and no treatment effect has been reported.

The two count outcomes of interest were the number of times falling asleep while driving and the number of falls. The SAP stated that these outcomes would be analysed using a Poisson model and if there were excess zeros and/or over-dispersion in the data, a zero-inflated Poisson model and/or a negative binomial model would be considered instead. Both outcomes had excess zeros; < 10% of participants had one or more times falling asleep while driving or number of falls. Due to the event rates being low, a simpler analysis was undertaken instead. These outcomes were defined as a binary outcome [no (0 events)/yes (1 + events)], and a logistic mixed-effect model was used.

Serious adverse events were analysed based on the number of participants who actually received the intervention and Fisher’s exact test was used to compare SRT and SH.

Missing data and sensitivity analyses. The following sensitivity analyses were pre-specified in the SAP to examine the robustness of the primary outcome results to different assumptions regarding missing data:

1. analysis adjusted for baseline covariates found to be predictive of missingness

2. exclusion of any self-rated insomnia severity scores from the analysis which were deemed to be outliers (none were observed)

3. analysis using pattern mixture model to examine the robustness of the missing at random assumption

4. analysis for missing data on the primary outcome at 6 months assuming plausible arm-specific differences between responders and non-responders.

Full details of the sensitivity analyses were specified in the SAP. Multiple imputation of the primary outcome analysis was also conducted as a post hoc sensitivity analysis.

Moderation analyses. We conducted pre-specified subgroup analysis of the primary outcome by baseline actigraphy-defined sleep duration (< 6 vs. ≥ 6 hours), sleep medication use, depression severity (PHQ-9), age, level of deprivation, and chronotype [assessed with the morningness–eveningness questionnaire, reduced version (MEQr)]. 54 The subgroup analyses were conducted using the same method above but adding a three-way interaction term between randomised group, assessment time point, and a subgroup indicator variable to allow the treatment effect to be estimated at each time point and in each level of the subgroups.

Mediation analyses. We proposed in the statistical analysis plan to use structural equation modelling for the mediation analyses; however, due to convergence problems, the analysis strategy was revised and conducted using the Baron and Kenny55 approach but adapted to make use of linear mixed-effect models (similar to Freeman et al. 56). A mixed effects model was fitted to estimate the mediator-outcome effect and another mixed effects model to estimate the treatment-mediator effect. The indirect effect was then calculated as the product of the effect of the mediator at 3 months on outcome at 6 months and the effect of treatment on mediator at 3 months. Confidence intervals and p-values were calculated using Sobel’s test. This allowed us to determine the extent to which the 3-month arousal and sleep effort outcomes (PSAS, GSES) mediated the 6-month ISI outcome. All models included baseline assessments of the mediator and ISI as covariates.

Compliance and adherence. A complier-average causal effect (CACE) analysis of the primary outcome was carried out to determine the impact of compliance with the allocated intervention on the treatment effect. Compliance was defined as attending at least one treatment session. CACE models were estimated using an instrumental variable approach where the outcome is total ISI score at 6 months adjusted for baseline ISI. Additionally, models were fitted adjusting for baseline characteristics that appeared to be associated with compliance. Sensitivity analyses were carried out which adjusted the definition of compliance to attending at least two, three or four sessions, and multiple imputation was carried out on the primary CACE analysis as a sensitivity analysis to assess the impact of missing data.

We also explored the effect of level of adherence to prescribed bed and rise times (captured by sleep diaries) on the primary outcome in those who received SRT. Percentage treatment adherence was categorised (≥ 0 to ≤ 40/> 40 to ≤ 60/> 60 to ≤ 80/> 80 to ≤ 100) and descriptive estimates for the ISI at 6 months (primary end point), change from baseline to 3 months, and change from baseline to 6 months are presented for each category. Treatment effects on the change scores for different levels of adherence were estimated by fitting a group by categorised adherence interaction in the model, with the reference category being the control group. The models are adjusted for baseline ISI score and a random effect is fitted for practice. Therefore, these estimated treatment effects reflect difference in the change in ISI from baseline for each adherence category as compared to control.

All analyses were conducted using Stata (version 16.1).

Patient and public involvement

Four people from the Healthier Ageing Public and Patient Involvement group, University of Lincoln, read and provided detailed comments on the original grant proposal, helping to shape key methodological choices. For example, the group recommended adding a patient-centred measure of quality of life and assessing long-term follow-up of sleep and daytime functioning outcomes. Two individuals, one with experience of insomnia and SRT, contributed during the conduct of the trial by reviewing the participant information sheet, consent form, therapy workbooks and questionnaire measures. They recommended amendments to improve the readability and accessibility of all participant-facing documents. They also advised on recruitment procedures and methods to engage prospective participants and retain enrolled participants, and were members of the Trial Steering Committee (TSC) who met every 6 months during the trial. They supported interpretation of findings and will advise on dissemination of findings once published.

Ethical approval

The trial received both Health Research Authority approval (IRAS: 238138) and ethical approval (Yorkshire and the Humber – Bradford Leeds REC, reference: 18/YH/0153).

Summary of changes to the project protocol

Table 3 summarises the key changes made to the protocol during the trial.

Recruitment

This chapter uses material from an Open Access article previously published by the research team [see Kyle SD, Siriwardena AN, Espie CA, Yang Y, Petrou S, Ogburn E, et al. Clinical and cost-effectiveness of nurse-delivered sleep restriction therapy for insomnia in primary care (HABIT): a pragmatic, superiority, open-label, randomised controlled trial. Lancet 2023;402(10406):975–87. https://doi.org/10.1016/S0140-6736(23)00683-9. Epub

10 Aug 2023. PMID: 37573859]. This article is published under licence to The Lancet. This is an Open Access article distributed in accordance with the terms of the Creative Commons Attribution (CC BY 4.0) licence, which permits others to distribute, remix, adapt and build upon this work, for commercial use, provided the original work is properly cited. See: https://creativecommons.org/licenses/by/4.0/.

We recruited participants from 35 practices (average patient list size = 11,802) across three sites (Thames Valley, Greater Manchester, Lincolnshire) between 29 August 2018 and 23 March 2020. A total of 31,464 invitation letters were sent out from practices; 3171 people entered the screening phase and 642 participants were randomised (321 to intervention and 321 to control; Figure 1). Main reasons for exclusion following eligibility assessment were not meeting insomnia criteria, shift work and suspected sleep disorder other than insomnia (see Appendix 1, Table 33).

FIGURE 1.

Participant flow chart.

Baseline data

Baseline characteristics by randomised group are presented in Tables 4–6. Mean age (range) was approximately 55 (19–88) years old, 76% were female, 97% were from a white ethnic background, and nearly 50% had a university degree. Mean (SD) ISI scores were in the clinical range (17.5–4.1), median duration of insomnia was 10 years, 76% had previously consulted their doctor for insomnia, and 25% reported current use of prescribed sleep medication. The sample had a range of comorbid conditions. For example, 41% had a mental health problem, 30% had a musculoskeletal disorder and 20% had a respiratory illness. Seventy-one per cent had two or more medical conditions. Consistent with these data, mean SF-36 scores for mental health and physical health were lower than normative values58 and 49% met ‘caseness’ for depression on the PHQ-9 (score ≥ 10). Baseline characteristics were similar between the two groups, with a slightly higher percentage of participants in the SRT group having consulted for insomnia (78% vs. 74% for SH).

Treatment receipt and fidelity

Fidelity of sleep restriction therapy sessions

Seventy-nine audio recordings of therapy sessions (53 session 1, 26 session 3) were sampled and reviewed by a clinical psychologist experienced in sleep medicine. Fidelity ratings were high for session 1 [median % = 100, interquartile range (IQR) 96.2–100] and session 3 (median % = 87.5, IQR 75–100).

Numbers analysed

Table 9 summarises data on completion of follow-up assessments, withdrawals (and reasons) and analysis population. Five hundred and eighty participants (90.3%) provided data at a minimum of one follow-up time point.

Table 10 summarises the availability of data for the primary and secondary outcomes at each time point by randomised group and overall. Eighty-five per cent of participants provided data on the primary outcome (ISI) at 6 months post randomisation. Of note, data completion for sleep diaries and actigraphy at 6 and 12 months was low (≤ 41%), chiefly due to the pandemic, which precluded sending out watches and diaries. Data on absenteeism, presenteeism and work productivity loss (from the WPAI) were only available for those in employment.

Table 11 shows that randomised group was associated with missingness of the primary outcome, with the SRT more likely to have missing data at 3, 6 and 12 months post randomisation.

Outcomes and estimation

Primary outcome

The primary objective of the HABIT trial was to compare the effect of SRT versus SH on insomnia severity (assessed by the ISI) at baseline and 3, 6 and 12 months post randomisation. The primary end point was the 6-month time point.

Table 12 summarises the adjusted treatment effect at each time point from the linear mixed-effect model (Figure 2). At 6 months post randomisation, the estimated adjusted mean difference on the ISI was −3.05 (95% CI −3.83 to −2.28; p < 0.001, Cohen’s d = 0.74), indicating that participants in the SRT arm reported lower insomnia severity compared to the SH group. Treatment effects were also evident at 3 and 12 months. Mean differences between arms were reflected in the number of participants showing a treatment response (ISI change score reduction ≥ 8 points) and scoring in the non-clinical range (ISI absolute score < 11). At 6 months, 42% (108/257) of the SRT group met criteria for a clinically significant treatment response, while only 17% (49/291) of the SH arm did. Fifty per cent (128/257) of the SRT arm were in the non-clinical range at 6 months compared with 28% (80/291) in the SH arm.

TABLE 12 - Adjusted treatment effect for the primary outcome (insomnia severity)

SRT vs. SH.

Level of significance = 0.05.

Cohen’s d = adjusted treatment effect divided by the sample SD at baseline.

Linear mixed-effect model with an unstructured variance–covariance structure for the random effects, modelled against randomised group, outcome score at baseline, minimisation factors (baseline ISI score, region, age, use of prescribed sleep-promoting medication, sex, and baseline PHQ-9 score), assessment time point, and an interaction between randomised group and assessment time point as fixed effects; GP practice as a random effect, and a random intercept for each participant.

Primary outcome.

	SRT (N = 321)	SH (N = 321)	Adjusted treatment difference (95% CI)a	p-valueb	Cohen’s dc
Primary analysis
Self-rated insomnia severity, mean (SD) (n)d
3 months	10.9 (5.47) (252)	14.8 (5.11) (283)	−3.88 (−4.66 to −3.10)	< 0.001	−0.95
6 monthse	10.9 (5.51) (257)	13.9 (5.23) (291)	−3.05 (−3.83 to −2.28)	< 0.001	−0.74
12 months	10.4 (5.89) (233)	13.5 (5.52) (275)	−2.96 (−3.75 to −2.16)	< 0.001	−0.72

FIGURE 2.

Changes in the primary outcome, insomnia severity, across groups and time points. Raw means (±SD) are presented for both groups at each time point.

We performed sensitivity analyses to assess missingness of the primary outcome (ISI). Table 13 shows the results for the primary outcome when (1) adjusting for characteristics associated with non-completion of the ISI at 6 months and (2) performing multiple imputation. Both models yielded similar estimates as the primary analysis, demonstrating superiority of SRT over SH. A pattern mixture model was also conducted where missing ISI outcome values were imputed by up to five points either side of the observed average, both overall and in the SRT and SH arms separately. Even under these conservative assumptions the treatment effect and 95% CI would still not include 0 (see Appendix 2, Figure 21). Analyses assuming informative missingness of insomnia severity scores at 6 months [i.e. data missing not at random (MNAR)] indicated that even with asymmetrical differences between responders and non-responders conclusions are similar to the primary analysis (Appendix 2, Table 34).

TABLE 13 - Sensitivity analyses of the primary outcome at 6 months

SRT vs. SH.

Level of significance = 0.05.

Primary outcome.

	SRT	SH	Adjusted treatment difference (95% CI)a	p-valueb
	(N = 321)	(N = 321)
Self-rated insomnia severity, mean (SD) (N)
Adjusting for characteristics associated with non-completion of ISI
3 months	10.9 (5.47) (252)	14.8 (5.11) (283)	−3.64 (−4.42 to −2.85)	< 0.001
6 monthsc	10.9 (5.51) (257)	13.9 (5.23) (291)	−2.83 (−3.61 to −2.05)	< 0.001
12 months	10.4 (5.89) (233)	13.5 (5.52) (275)	−2.71 (−3.50 to −1.91)	< 0.001
Multiple imputation
3 months	11.4 (5.86) (321)	15.0 (5.25) (321)	−3.86 (−4.63 to −3.08)	< 0.001
6 monthsc	11.3 (5.88) (321)	14.1 (5.40) (321)	−3.03 (−3.78 to −2.29)	< 0.001
12 months	11.1 (6.86) (321)	13.7 (5.75) (321)	−2.84 (−3.66 to −2.01)	< 0.001

Complier-average causal effects analyses

Baseline characteristics are presented for compliers and non-compliers in the treatment arm (Table 16). Compliance was defined as attending at least one SRT session.

Table 17 summarises complier average causal effects for those attending a minimum of one, two, three, and four treatment sessions, respectively. Results show that attending more treatment sessions was associated with a larger treatment effect, relative to the primary analysis. For example, there is a > 1-point difference in the treatment effect on the ISI for those attending all four sessions (−4.10, 95% CI −5.06 to −3.14) versus the primary analysis (−3.05, 95% CI −3.83 to −2.28).

Adherence to sleep restriction therapy

Implementation of SRT was indexed using self-reported bed and rise times from sleep diaries completed during the 4-week intervention. A percentage score was calculated for each participant, reflecting the number of bed and rise times adhered to within 15 minutes of the nurse prescription. One hundred and fifty-seven participants (49%) returned intervention diaries; 164 participants did not return diaries or returned incomplete diaries (i.e. < 50% of days with relevant questions completed). Mean adherence for returned diaries was 76.4% (SD = 21.6), with the majority of participants categorised as 60–100% adherent (Table 18).

Treatment effects on the change scores for different levels of adherence were estimated by fitting a group by adherence interaction in the model, with the reference category being the control group. The models are adjusted for baseline ISI score and a random effect was fitted for GP practice. Estimated treatment effects therefore reflect the difference in the change in ISI scores from baseline for each adherence category as compared to control.

At 6 months, those with higher diary-defined SRT adherence tended to display greater change from baseline and stronger estimated treatment effects. At 3 months the pattern appeared non-linear, with adherence categories > 40–≤ 60/> 60–≤ 80/> 80–≤ 100 separating and exhibiting stronger treatments relative to the 0–40% category.

Mediation and moderation analyses

Our proposed mediators, pre-sleep arousal (PSAS) and sleep effort (GSES), were significantly reduced in the SRT group relative to control at 3 months post randomisation (see Table 14). The extent to which these variables causally mediated 6-month ISI was investigated using the approach of Baron and Kenny adapted for linear mixed-effect models. Tables 19–21 summarise the direct and indirect effects for each mediator separately. There were statistically significant indirect effects for sleep effort, pre-sleep cognitive arousal and somatic arousal, which mediated between 15% and 36% of the total treatment effect at 6 months.

We performed exploratory moderation analyses on the following subgroups at baseline for the ISI at 6 months:

• actigraphy-defined TST at baseline, categorised as either < 6 or ≥ 6 hours

• chronotype (morning, intermediate or evening) defined by the MEQr at baseline

• age (18–65 years vs. > 65 years)

• patient-reported prescribed sleep medication use at baseline (Yes vs. No)

• depression ‘caseness’ (PHQ-9 score < 10 vs. ≥ 10)

• socialeconomic deprivation [Index of Multiple Deprivation (IMD) score: National quartiles 1 and 2 vs. 3 and 4].

Figure 3 summarises the adjusted mean differences between the randomised groups at 6 months for each level of the subgroup and the test of interaction. There were no significant subgroup differences for TST, chronotype, depression severity, age, sleep medication use, or level of deprivation.

FIGURE 3.

Forest plot of the results from the subgroup analyses.

Adverse events

Pre-defined AEs (work-related accidents, falls, motor-vehicle accidents, near-miss driving incidents, falling asleep while driving) were assessed at baseline, 3, 6 and 12 months. Logistic mixed-effect models revealed no differences between groups for any outcome at any time point (Table 22).

Serious adverse events

The number of SAEs is presented in Table 23. In total, 16 participants (8 in each arm) experienced at least one SAE. There was one death per group [one due to major haemorrhage (SH) and one due to pneumonia (SRT group)]. None of the SAEs were deemed to be related to the intervention or study.

Impact of COVID-19

The final participant was randomised on 23 March 2020, which was the start date for the national UK lockdown due to COVID-19. The trial was able to continue with remote data collection for most outcomes during the pandemic. Sleep diaries and actigraphy watches were not sent out during lockdown because the research team could not access university buildings; this led to low completion rates for sleep diary, actigraphy and medication use outcomes. A small number of participants in the SRT arm were directly affected by the pandemic (n = 13) such that treatment sessions were adjusted so that they could be completed remotely. Because the lockdown and pandemic may have adversely affected sleep, a sensitivity analysis was conducted to explore whether there was a difference in treatment effect on the ISI between participants who completed the 6-month follow-up before the pandemic (< 23 March 2020) compared with participants whose follow-up was completed during the pandemic (≥ 23 March 2020). There was no evidence that treatment effects differed pre versus during the pandemic (see Appendix 3, Table 35).

Introduction

This chapter uses material from an Open Access article previously published by the research team [see Kyle SD, Siriwardena AN, Espie CA, Yang Y, Petrou S, Ogburn E, et al. Clinical and cost-effectiveness of nurse-delivered sleep restriction therapy for insomnia in primary care (HABIT): a pragmatic, superiority, open-label, randomised controlled trial. Lancet 2023;402(10406):975–87. https://doi.org/10.1016/S0140-6736(23)00683-9. Epub 10 Aug 2023. PMID: 37573859]. This article is published under licence to The Lancet. This is an Open Access article distributed in accordance with the terms of the Creative Commons Attribution (CC BY 4.0) licence, which permits others to distribute, remix, adapt and build upon this work, for commercial use, provided the original work is properly cited. See: https://creativecommons.org/licenses/by/4.0/.

This chapter presents the health economic evaluation conducted as part of the HABIT trial. The base-case analysis took an NHS and PSS perspective and assessed the cost-effectiveness of nurse-delivered SRT relative to SH alone for insomnia in primary care. Health care and PSS resource utilisation data and EQ-5D-3L utility data were collected alongside clinical data. These data were used to conduct a cost–utility analysis, calculating the incremental cost per QALY gained during the 12-month trial period as the primary outcome of the economic analysis. Sensitivity analyses were conducted to explore how the result was affected by altering several key features of the economic evaluation, including (1) complete-case analysis without data imputation, (2) adopting a societal perspective and (3) adjusting the nurse training cost for SRT. Pre-specified secondary exploratory analyses were also conducted: (1) using two other utility measures (SF-6D and EQ-5D + Sleep) to calculate QALYs, (2) only including participants who attended at least one SRT session in the intervention arm for the per-protocol analysis, (3) using only NHS and PSS costs and EQ-5D-3L data over the first 6 months of follow-up and (4) using improvement of ISI scores and treatment response measured by ISI change score as health outcomes.

We followed current guidelines59,60 for conducting and reporting economic evaluations within clinical trials, including in relation to the design, conduct, data analysis and reporting.

Methods

Results

Cost-effectiveness and cost–utility analysis

Table 31 reports results from the base-case cost–utility analysis, sensitivity analyses and secondary exploratory analyses. The base-case analysis was conducted from an NHS and PSS perspective and used NHS and PSS costs and QALYs (obtained from the EQ-5D-3L) over the 12-month follow-up, applying multiple imputation for missing data and controlling for baseline characteristics. It generated incremental costs of £43.59 (95% CI −18.41 to 105.59) and incremental QALYs of 0.021 (95% CI 0.0002 to 0.042) associated with SRT relative to SH. This resulted in a mean ICER of £2076 per QALY gained. The probability that the SRT is cost-effective at the NICE cost-effectiveness threshold of £20,000 per QALY gained was 95.3%, with a mean NMB of £377.84. The probabilities that SRT is cost-effective at the NICE cost-effectiveness threshold of £15,000 and £30,000 per QALY were 94.4% and 96.2%, with respective mean NMBs of £272.12 and £589.28. The cost-effectiveness plane (Figure 4) displays graphically the uncertainty surrounding the mean ICER estimate, while the CEAC (Figure 5) summarises the effects of uncertainty surrounding the value of the cost-effectiveness threshold.

FIGURE 4.

Cost-effectiveness plane representing bootstrapped mean differences in costs and QALYs for SRT compared with SH (NHS and PSS costs and QALYs based on EQ-5D-3L).

FIGURE 5.

Cost-effectiveness acceptability curve for the base-case analysis (NHS and PSS costs and QALYs based on EQ-5D-3L).

TABLE 31 - Incremental cost-effectiveness ratio at 12-month follow-up for base-case analysis, sensitivity analyses and secondary analyses

SE, standard error.

Seemingly unrelated regression model was used. Baseline covariates included for NHS and PSS costs: age, sex, study site, ISI scores, PHQ-9 scores, whether taking insomnia medication at baseline, EQ-5D-3L utility scores (for QALYs) and NHS and PSS cost 3 months before baseline. Baseline covariates included for QALYs: age, sex, study site, ISI scores, PHQ-9 scores, whether taking insomnia medication at baseline, EQ-5D-3L utility score at baseline.

Models and covariates are the same as ^a except baseline EQ-5D-3L + Sleep utility values were used rather than baseline EQ-5D-3L utility values.

Models and covariates are the same as ^a except baseline SF-6D utility values were used rather than baseline EQ-5D-3L utility values.

Scenario	Mean cost (£) (SE)			Mean QALY (SE)			ICER (£)	Probability that SRT is cost-effective at NICE cost-effectiveness thresholds			Mean NMB (95% CI) at NICE cost-effectiveness threshold
	SRT	SH	Incremental cost (bootstrap 95% CI)	SRT	SH	Incremental QALYs (bootstrap 95% CI)		£15,000 (%)	£20,000 (%)	£30,000 (%)	£15,000	£20,000	£30,000
Scenario	Mean cost (£) (SE)			Mean ISI score (SE)			ICER (£)	Probability that SRT is cost-effective at arbitrary cost-effectiveness thresholds			Mean NMB (95% CI) at arbitrary cost-effectiveness threshold
	SRT	SH	Incremental cost (bootstrap 95% CI)	SRT	SH	Incremental ISI score (bootstrap 95% CI)		£15	£30	£50	£15	£30	£50
Base-case analysis
NHS and PSS cost and QALYs based on EQ-5D-3L [multiple imputation (n = 50); covariates adjusted]a	266.00 (25.55)	222.41 (26.24)	43.59 (−18.41 to 105.59)	0.723 (0.008)	0.702 (0.008)	0.021 (0.0002 to 0.042)	2076	94.4	95.3	96.2	272.12 (261.59 to 282.65)	377.84 (364.06 to 391.62)	589.28 (568.96 to 609.60)
Sensitivity analyses
NHS and PSS cost and QALYs based on EQ-5D-3L (complete-case analysis; covariates adjusted)	252.35 (28.41)	199.23 (25.45)	53.12 (−20.00 to 126.23)	0.742 (0.009)	0.726 (0.008)	0.017 (−0.007 to 0.041)	3125	85.8	88.0	89.7	207.96 (195.93 to 219.98)	295.02 (279.23 to 310.81)	469.15 (445.77 to 492.52)
Societal cost and QALYs using EQ-5D-3L [multiple imputation (n = 50); covariates adjusted]	2340.62 (189.56)	3426.75 (186.21)	−1086.13 (−1485.59 to −686.67)	0.723 (0.008)	0.702 (0.008)	0.021 (0.0003 to 0.042)	Dominates	100	100	100	1404.30 (1387.82 to 1420.77)	1510.54 (1491.78 to 1529.30)	1723.03 (1698.99 to 1747.06)
NHS and PSS cost using £2.52 as SRT training cost and QALYs using EQ-5D-3L [multiple imputation (n = 50); covariates adjusted]	236.82 (25.55)	222.41 (26.24)	14.41 (−47.59 to 76.41)	0.723 (0.008)	0.702 (0.008)	0.021 (0.0002 to 0.042)	686	96	96.30	97	301.30 (290.77 to 311.83)	407.02 (393.24 to 420.80)	618.46 (598.14 to 638.78)
Secondary analyses
NHS and PSS cost and QALYs based on EQ-5D + Sleep [multiple imputation (n = 50); covariates adjusted]b	266.22 (25.55)	222.20 (26.23)	44.02 (−17.93 to 105.97)	0.789 (0.005)	0.767 (0.005)	0.022 (0.010 to 0.034)	2001	99.6	99.9	100	281.58 (275.32 to 287.84)	390.58 (382.51 to 398.64)	608.57 (596.83 to 620.31)
NHS and PSS cost and QALYs based on SF-6D [multiple imputation (n = 50); covariates adjusted]c	266.19 (25.55)	222.23 (26.23)	43.95 (−17.88 to 105.78)	0.666 (0.004)	0.642 (0.004)	0.025 (0.015 to 0.034)	1758	100	100	100	324.36 (319.35 to 329.37)	447.58 (441.19 to 453.97)	694.03 (684.81 to 703.25)
NHS and PSS cost and QALYs based on EQ-5D-3L (per-protocol analysis) [multiple imputation (n = 50); covariates adjusted]	257.25 (25.67)	220.86 (26.17)	36.40 (−27.72 to 100.52)	0.722 (0.009)	0.703 (0.008)	0.019 (0.00009 to 0.038)	1916	92.3	94.9	95.9	256.72 (247.01 to 266.43)	353.97 (341.28 to 366.67)	548.47 (529.76 to 567.19)
NHS and PSS cost and QALYs based on EQ-5D-3L (6-month follow-up) [multiple imputation (n = 50); covariates adjusted]	198.37 (18.36)	126.60 (17.01)	71.76 (31.94 to 111.59)	0.362 (0.004)	0.347 (0.004)	0.015 (0.006 to 0.025)	4784	97.6	98.7	99.8	158.38 (153.47 to 163.28)	235.13 (228.74 to 241.53)	388.65 (379.24 to 398.05)
NHS and PSS cost and ISI improvement between baseline and 12-month follow-up [multiple imputation (n = 50); covariates adjusted]	270.68 (29.41)	226.24 (27.91)	44.43 (−28.93 to 117.80)	−6.90 (0.32)	−3.74 (0.29)	−3.16 (−4.04 to −2.28)	14	52.1	88.1	99.7	£1.95	£49.51	112.92

All sensitivity analyses confirmed the robustness of the result that SRT is likely to be cost-effective at a cost-effectiveness threshold of £20,000 per QALY (see Table 31 and Figures 6–11). Indeed, when the societal perspective was used for the analysis, SRT cost less and generated more QALYs, on average, and so dominates SH in health economic terms. When the SRT training cost was reduced to £2.52 from £31.7, the ICER reduced to £686 per QALY gained (from £2076 in the base-case analysis).

FIGURE 6.

Cost-effectiveness plane: bootstrapped mean differences in costs and QALYs (NHS and PSS costs and QALYs based on EQ-5D-3L, complete-case analysis).

FIGURE 7.

Cost-effectiveness acceptability curve (NHS and PSS costs and QALYs based on EQ-5D-3L, complete-case analysis).

FIGURE 8.

Cost-effectiveness plane: bootstrapped mean differences in costs and QALYs (societal costs and QALYs based on EQ-5D-3L).

FIGURE 9.

Cost-effectiveness acceptability curve (societal costs and QALYs based on EQ-5D-3L).

FIGURE 10.

Cost-effectiveness plane: bootstrapped mean differences in costs and QALYs (NHS and PSS costs using £2.52 as SRT training costs, and QALYs based on EQ-5D-3L).

FIGURE 11.

Cost-effectiveness acceptability curve (NHS and PSS costs using £2.52 as SRT training costs, and QALYs based on EQ-5D-3L).

Secondary analyses (see Table 31 and Figures 12–20) also demonstrated that SRT is likely to be cost-effective when other utility measures were used, applying per-protocol analysis (those attending at least one treatment session), and using data for 6 months follow-up only. When the cost–utility analysis was repeated for the SF-6D and EQ-5D-3L, the point estimates of cost-effectiveness were very similar to those using the EQ-5D-3L, although the 95% CIs were smaller. After taking account of uncertainties, the SF-6D produced a stronger conclusion; that SRT has a 100% probability of being cost-effective at the cost-effectiveness threshold of £20,000 per QALY. The probability of cost-effectiveness when using the EQ-5D-3L + Sleep was also higher than that of the EQ-5D-3L (99.9% probability of being cost-effective at a cost-effectiveness threshold of £20,000 per QALY).

FIGURE 12.

Cost-effectiveness plane: bootstrapped mean differences in costs and QALYs (NHS and PSS costs and QALYs based on EQ-5D-3L + Sleep ‘bolt on’).

FIGURE 13.

Cost-effectiveness acceptability curve (NHS and PSS costs and QALYs based on EQ-5D-3L + Sleep ‘bolt on’).

FIGURE 14.

Cost-effectiveness plane: bootstrapped mean differences in costs and QALYs (NHS and PSS costs and QALYs based on SF-6D).

FIGURE 15.

Cost-effectiveness acceptability curve (NHS and PSS costs and QALYs based on SF-6D).

FIGURE 16.

Cost-effectiveness plane: bootstrapped mean differences in costs and QALYs (NHS and PSS costs and QALYs per-protocol analysis).

FIGURE 17.

Cost-effectiveness acceptability curve (NHS and PSS costs and QALYs per-protocol analysis).

FIGURE 18.

Cost-effectiveness plane: bootstrapped mean differences in costs and QALYs (NHS and PSS costs and QALYs at 6-month follow-up).

FIGURE 19.

Cost-effectiveness acceptability curve (NHS and PSS costs and QALYs at 6-month follow-up).

FIGURE 20.

Cost-effectiveness plane: bootstrapped mean differences in costs and QALYs (NHS and PSS costs and reduction of ISI scores between baseline and 12-month follow-up).

Furthermore, restricting the time horizon of the economic evaluation suggested that SRT remains cost-effective over 6 months post randomisation (ICER of £4784), but not as cost-effective as over 12 months post randomisation.

The ICER was estimated at £14 per unit reduction in ISI when reduction of ISI score was used as the measure of effectiveness. At a hypothetical cost-effectiveness threshold of £30 per unit reduction in ISI, SRT had a probability of cost-effectiveness of 88.1%.

For treatment response (defined as ISI reduction of ≥ 8 points), the mean incremental cost was £44.23 and the mean incremental probability of a treatment response was 0.26 with an ICER of £170, indicating a mean incremental cost of SRT of £170 is required to achieve a clinically relevant treatment response.

Conclusion

The economic analysis within the HABIT trial evaluated the cost–utility of SRT compared with SH in the NHS primary care setting. The analysis quantified the mean cost of SRT as £84, although the initial training costs are likely to reduce following scaling-up of the intervention, or delivery via alternative methods. Further implementation research is needed to consider how nurse-delivered SRT would operate in practice. For example, nurses were trained by experienced members of the research team but in practice we envisage that training and ongoing support could be provided by a clinical psychologist, or mental health professional with experience in sleep disorders and cognitive–behavioural approaches.

The primary cost–utility analysis used EQ-5D-3L-derived QALYs and NHS and PSS costs over the 12-month follow-up. Based on available data, the SRT arm produced a mean QALY of 0.73 versus 0.72 for the SH arm. After data imputation and adjustment for baseline covariates, the mean difference in QALYs between the two arms over the 12-month follow-up period was estimated at 0.02. Although the mean QALY gain is not large, the ICER was estimated at £2076 per QALY gained, which suggests great potential for SRT to be cost-effective at the NICE £20,000 per QALY cost-effectiveness threshold. Further exploration of the decision uncertainty around the estimate of mean ICER showed that SRT has a 95.3% probability of being cost-effective at a £20,000 cost-effectiveness threshold, and indeed a 94.4% probability of being cost-effective at a £15,000 cost-effectiveness threshold. Sensitivity analysis using the available sample with no imputation also confirmed the cost-effectiveness of SRT, although the mean ICER was larger relative to the baseline analysis that applied multiple imputation. When adjusting the SRT training cost, the mean ICER decreased from £2076 to £686. SRT had the effect of reducing productivity-related losses, which was reflected in the sensitivity analysis that adopted a societal perspective where SRT dominates SH.

The exploratory analysis using QALYs derived from the EQ-5D-3L and the SF-6D confirmed the conclusion that SRT is highly likely to be cost-effective, and the probabilities of SRT being cost-effective are higher using the EQ-5D-3L + Sleep and the SF-6D than using the EQ-5D-3L. Restricting the economic evaluation to a 6-month time horizon also confirms that SRT is highly likely to be cost-effective, but not as cost-effective as when a longer time horizon is adopted.

Methods

Results

The initial aim was to recruit five practices per region with equal numbers of interviews of patients, nurses and practice managers or GPs from each. We interviewed 16 patients, 13 nurses and 7 practice managers or GPs. Interviews were conducted by telephone and were 30–60 minutes in duration. Patients ranged in age from 19 to 74 (mean 56) years, including 7 male and 9 female interviewees, all of whom identified as White British. Patients are designated in the results by region (A, B, C), gender (M, F) and age, for example Patient AF57. Nurses are designated by region and whether they were a Clinical Research Network (CRN) nurse or a practice nurse (PN).

Due to lack of availability of nurses at specific practices two regions utilised research nurses (employed by their LCRN) rather than practice nurses. ICRN research nurses covered more than one practice and therefore 13 nurse participants were interviewed. Finally, in two regions practices formed consortia, with several practices falling under one management group, so seven interviews were undertaken in the practice manager (six interviews) or GP (one GP) category.

Themes are listed under implementation, mechanisms of impact and contextual factors.

Discussion

The aim of the process evaluation was to establish the experiences and perceptions of patients, nurses, and GPs or practice managers of SRT as part of the HABIT trial and to investigate how SRT was received and delivered, understand why it worked or did not, and explore facilitators or barriers to implementation that may affect wider use of this treatment in primary care, should the intervention prove effective.

Both patients and nurses reported that they were able to quickly grasp the purpose of SRT and the related processes. Patients preferred face-to-face consultations and felt that these helped maintain motivation. Although face-to-face interactions have been found to be preferred in some studies, overall the evidence is lacking that therapeutic alliance, disclosure, empathy, attentiveness or participation differs in face-to-face compared with telephone delivery of psychological interventions. 68 Some patients found calculating SE difficult and felt that they needed help from the nurse, while nurses pointed out that helping someone with maths over the telephone was harder than in person.

All patients interviewed found the first week of therapy difficult, with reduced time in bed and strict bedtime and rising times. This is consistent with previous evaluations of SRT, where participants reported worsening of daytime functioning in the first week, with improvements felt after a period of adjustment. 69,70 Additionally, it has been found that restriction of time in bed, which leads to transient daytime sleepiness and related side effects, outperforms regular bed and rise times without restriction. 25,26 This suggests that while the initial increase in side effects is challenging it may also be a necessary part of the therapy.

In this study there was negotiation between the nurses and the patients regarding sleep times and the need for flexibility, which was supported to some extent by the protocol. 1 Changing ingrained behaviours, in this case fixed night-time (or daytime nap) routines, was challenging and the flexibility on the part of the nurses allowed patients to feel some level of control. The flexibility built into the protocol meant that these did not affect the fidelity of delivery. Fidelity was found to be high by the independent reviewer. One nurse interviewed did mention sharing delivery of the intervention with a colleague for one patient, which would only be problematic if inconsistent advice was given.

Participants reported adverse effects such as increased tiredness, ‘exhaustion’ and worries about driving, which have been found in other studies. 69,70 For some, these experiences led them to discontinue SRT (Table 8). Other reported confounding factors, external to the intervention, included sleep disturbance due to menopause symptoms and the use of sleep aids (such as sedatives) which extended the allocated sleep time. These factors should be considered in the future rollout of SRT.

Patients who experienced improved SE also reported concerns, most commonly that 4 weeks of SRT was not long enough. All participants found the first week of the intervention very difficult as their body adjusted to limited time in bed. By the third week some were seeing significant benefits. For example, one participant spoke of being woken by their alarm for the first time in years. Others only started to see benefits by the final week and as such felt the loss of support at the end of the intervention had a direct impact on their motivation to continue. Those who saw improvements earlier tended to be more likely to continue after the final therapy session, while those that felt the benefit later were more likely to revert to previous habits. One patient reported taking a nap in the afternoon the day after the final session and that they quickly reverted to their previous habits as there was no-one ‘watching over them’ any more. This is reflected in the joint display (see Table 32), where comparisons between recorded improvements in sleep and the qualitative data suggest that participants who felt they were better able to apply the SRT intervention showed more improvement than those who struggled or needed more time and support. This is a significant finding that indicates the importance of individual/personalised delivery with regular check-ins continuing for some until the new habits and sleep patterns have been reinforced.

Previous research suggested it was possible for a single GP to deliver a modified version of SRT in general practice to patients without comorbidity,28 and this study confirmed that it was possible for nurses to deliver the intervention in a consistent manner across multiple practices. Practice managers and GPs also agreed that the intervention could be successfully delivered by nurses in this setting, which they considered may free up time for GPs. Several suggestions were put forward regarding how the intervention could be rolled out more widely. Practice managers suggested setting up specific clinics at set times in the week that could be run by healthcare assistants rather than practice nurses. It was also suggested that sessions could be run in small groups in a similar way to other behaviour-change clinics such as smoking cessation or weight-loss clinics. This is something that could be further explored in subsequent research.

Conclusions

We found that SRT can be successfully delivered by nurses in general practice and was generally well received by patients. Ongoing support after the initial intervention period could be assessed to determine whether this leads to improved adherence.

Clinical effectiveness

To our knowledge, HABIT is the largest randomised trial to date of a psychological treatment for insomnia delivered in a clinical setting. It is also one of the few controlled studies to follow up patients for 12 months. 71 Standardised effect sizes for the ISI were in the medium-to-large range at all time points, and multiple sensitivity analyses of the primary outcome suggest robustness to a range of assumptions regarding missingness. Descriptive data on treatment response (defined as ≥ 8 points on the ISI) parallel these changes (42% for SRT vs. 17% for SH at 6 months). Treatment effects exceed clinically significant thresholds defined by the American Academy of Sleep Medicine (AASM) Task Force on Behavioural and Psychological Treatments for Insomnia,38 as well as estimates from a recent meta-analysis of CBT-I trials performed within primary care (g = 0.40). 21 Moreover, pre-specified moderation analyses of the primary outcome revealed no significant effects for age, depression severity, chronotype, actigraphy-defined sleep duration, sleep-medication use, or level of deprivation, which is broadly consistent with meta-analyses looking at variability in effect sizes across trials. 72

While sleep diary data were available for only a minority of HABIT participants at follow-up, small-to-medium effects were found for sleep continuity variables (WASO, SE, SQ and TST) at both 6 and 12 months relative to control. Actigraphy-defined WASO and SE were also improved in the SRT group at 6 months, but not 12 months, and TST was reduced (by 13–15 minutes) at both time points. Results are broadly consistent with previous work showing that diary-recorded sleep is more sensitive to change following CBT relative to actigraphy. 73

In addition to improvements in insomnia we also observed treatment effects at all time points on several important secondary outcomes, including mental health-related and sleep-related quality of life, depressive symptoms, and work productivity and activity impairment. Effect sizes were in the small-to-medium range, consistent with meta-analysis of CBT for insomnia. 74 Treatment effects tended to be greater for patient-generated quality of life (GSII) relative to standardised measures (SF-36), presumably because the GSII is an idiographic measure, which increases signal-to-noise by measuring life domains important to each individual patient. 3,39 These results are important because the daytime consequences of insomnia are distressing for patients and the most common reasons for seeking treatment in primary care. 3,75 Effects on mental health outcomes are particularly noteworthy given the strong association between insomnia and psychiatric disorder. 76 For example, approximately 40% of the sample had a mental health condition at baseline and 49% met criteria for depression on the PHQ-9. Results suggest that targeting insomnia leads to a small and sustained reduction in depressive symptoms, which was also reflected in a reduction in depression ‘caseness’ (defined as PHQ-9 ≥ 10) between groups at 6 months (SRT = 29% vs. SH = 39%). While we did not specifically recruit a sample with depression, nor target depression during treatment, it is interesting that effect sizes appear similar in magnitude to those observed in trials of CBT for depression in primary care (assessing various delivery formats). 77 Given that insomnia is almost characteristic of depression, the specific management of insomnia through SRT may lead to improved mental health outcomes.

No group differences were found for number of nights of use, or proportion of participants using prescribed hypnotic or sedative medication at 6 or 12 months. Missing diary data due to the pandemic may have limited power to detect group effects for medication use; however, exploratory analysis of prescription data collected from practice records at 12-month follow-up also revealed similar proportions of participants in each arm being prescribed sleep-promoting hypnotic medication (SRT = 25.5% vs. SH = 25.1%). Conflicting findings have been observed in the CBT treatment literature,78 particularly for studies where hypnotic use was not an inclusion criterion, or where the intervention did not specifically have a focus on withdrawal or tapering of medication (both apply to the HABIT trial). It would be interesting to specifically test the effects of nurse-delivered SRT on long-term users of hypnotics, or alternatively investigate those first presenting to primary care with insomnia to ascertain whether offering SRT lessens prescriptions and use of sedative hypnotics.

HABIT is the first trial in the CBT field to rigorously measure SAEs and pre-defined AEs. 79 This was considered important because previous work has documented increased sleepiness, reduced psychomotor vigilance, and potential driving concerns during implementation of SRT,24,29,70 owing to the acute effects of restricted sleep opportunity. While participants reported challenges with sleepiness and fatigue during qualitative interviews (consistent with previous work29), we found no evidence that falls, accidents (including road traffic accidents and near misses) or sleepiness while driving were increased at any post-randomisation assessment. This was also the case for SAEs, which were infrequent, similar between arms, and not judged to be related to the intervention. Our nurse-delivered protocol emphasised to patients the importance of avoiding driving if sleepy. Moreover, nurses were able to modify the sleep window if participants reported concerns with excessive daytime sleepiness or experienced difficulties with adherence. Such flexibility in the delivery of SRT is important, particularly in routine clinical practice where patients have a range of comorbidities. Nevertheless, findings from the process evaluation suggested that participants still found the treatment challenging, prompting some participants to discontinue with the intervention. Descriptive data on reasons for withdrawal from intervention showed that 35 participants (11% of those randomised to SRT) discontinued due to lack of benefit or finding the intervention too challenging to implement.

It is known that SRT is the most challenging component of CBT for insomnia80–83 – yet potentially the most active. Restricted sleep opportunity is central to driving clinical outcomes,25,26 and HABIT data show stronger treatment effects for participants who attend more treatment sessions and more closely adhere to prescribed bed and rise times. It would be prudent, therefore, for future studies to test strategies that may improve treatment engagement and adherence. For example, one strategy that could be tested is the combination of light therapy and SRT. Bright light is known to have alerting properties84,85 and has been shown to reduce the impact of experimental sleep restriction on sleepiness and vigilance when administered during the day. 86–88 Moreover, light acts as the main zeitgeber for the synchronisation of the circadian rhythm. Regular and enhanced light exposure alongside a prescribed sleep opportunity may strengthen the circadian rhythm and help align homeostatic and circadian drives for sleep, a proposed mechanism of SRT. 23 Other potential refinements could include involving family members in treatment to support behaviour change and reduce obstacles to implementation,89 or prescription of a more gradual reduction of time in bed (sleep compression) for those who find SRT challenging.

While 92% of participants attended at least one out of four treatment sessions, 65% completed all four. Our numbers are consistent with or higher than other primary care trials of in-person CBT for insomnia20,31,90 and exceed rates of engagement found for other low-intensity interventions, such as digital CBT. 39,52,91–93 Qualitative interviews with nurses and patients also generated areas of potential refinement that could support treatment engagement. For example, digital technology (app and/or wearable device) could be blended with nurse-delivered SRT to automate recording and calculation of SE to reduce participant burden. Additional follow-up sessions with the nurse were suggested as a way to help maintain sleep behaviour change beyond the acute intervention phase. There is suggestive evidence from meta-analysis that > 4 sessions may yield enhanced treatment effect sizes72 but this must be balanced against cost and scalability in primary care, particularly when considered within a stepped care framework. Such refinements could be explored in future research, but it is worth noting that the proportion of participants achieving a treatment response in the present study (42%) is similar to a high-quality trial that assessed eight weekly sessions (45–60 minutes in duration) of behavioural therapy delivered by licensed or trainee clinical psychologists (44%). 94

The HABIT trial was not designed to evaluate treatment mechanisms, but we performed mediation analyses to enhance understanding of how SRT may exert its effects. Drawing on a theoretical model of SRT mechanism of action,23 we examined the mediating role of pre-sleep arousal and sleep effort on insomnia severity. SRT led to reductions in pre-sleep arousal and sleep effort at 3 months, which significantly (though modestly) mediated the treatment effect on the ISI at 6 months. Proportion mediated was larger for cognitive measures [sleep effort (36%), cognitive arousal (35%)] vs. self-reported somatic arousal (15%). Excessive pre-sleep arousal and sleep effort are reliable features of insomnia and may be involved in the maintenance of poor sleep via effects on autonomic and cortical arousal prior to and during the sleep period, which ultimately degrades sleep quality. Integrating previous experimental work25,29 with HABIT findings we hypothesise that enhancing sleep pressure and regularising time in bed reduce arousal and obviate sleep effort, leading to improved sleep consolidation. Improved sleep consolidation and quality then positively influence cognitive processes that operate during daytime periods (e.g. sleep-related worry and monitoring), which further lessens pre-sleep arousal and sleep effort in the evening. While this sequence and feedback loop needs to be appraised in dedicated studies – alongside other putative causal mechanisms – HABIT suggests that addressing arousal (especially cognitive arousal) and sleep effort may be important in lessening insomnia severity.

Cost-effectiveness

The HABIT trial was designed to test a scalable and potentially cost-effective treatment for insomnia in primary care. Health economic analysis showed that the cost of brief SRT was modest at £52.60 per trial participant and mean NHS and PSS costs (excluding intervention-related costs) were similar between arms over the 12-month period. In the primary analysis, mean NHS and PSS costs (including intervention-related costs) were just £43.59 (95% CI −18.41 to 105.59) higher in the SRT arm compared to control. Adjusting the SRT training cost to reflect what may happen in clinical practice (trained nurses seeing a much larger number of patients) led to a small difference of just £14.41 (−47.59 to 76.41). In terms of utility, the EQ-5D-3L showed a small difference of 0.021 in QALYs in favour of SRT. Nevertheless, small differences in both QALYs and costs produced an incremental cost-effective ratio of just £2075.71 per QALY with a high probability (95%) that the intervention is cost-effective at a cost-effectiveness threshold of £20,000 per QALY (NMB = £377.84). This was supported by a range of sensitivity analyses. Indeed, a probability of 94.4% of cost-effectiveness was estimated at a cost-effectiveness threshold of just £15,000. Poor sensitivity of the EQ-5D-3L to insomnia interventions has been reported in several trials,95–97 contrasting with effects for insomnia-specific outcomes like the ISI. In exploratory analyses we also performed cost–utility analyses using the SF-6D and EQ-5D-3L + Sleep. Both measures showed a small advantage in QALYs relative to control, and with slightly higher levels of decision certainty than the EQ-5D-3L (96.3% and 100% probability of being cost-effective at the £20,000 cost-effectiveness threshold).

HABIT is the largest trial to date to assess cost-effectiveness of a psychological treatment for insomnia and the only trial to assess costs and effectiveness over a 12-month horizon. Results provide robust support for the cost-effectiveness of nurse-delivered SRT. Our trial compares favourably to smaller studies adopting a similar approach but over a shorter time-frame, where probability of cost-effectiveness was 67% (at a £20,000 cost-effectiveness threshold) for guided digital CBT-I96 and just 34% (at a £30,000 cost-effectiveness threshold) for community-based CBT workshop delivery. 95 HABIT intervention costs are also lower than other low-intensity interventions that have been trialled in primary care [e.g. £148 for community-delivered workshops,95 £191 for counsellor-delivered CBT31 and £85 pounds (99 euros) for nurse-guided digital CBT96]. While SRT does not appear to be cost-saving for the NHS over a 12-month horizon (that is, resource use was broadly similar between arms), we did find that SRT dominated SH from a societal perspective with societal costs being reduced, on average, by £1086.13 (−1485.59 to −686.67) in the SRT arm compared to control. These differences principally reflected reduced productivity loss in the SRT arm. 98,99

We focused on self-reported health and social care resource use for insomnia and, as a consequence, there was a high degree of missing data compared to data extracted from practice records. Nevertheless, sensitivity analyses across both imputed and complete data sets led to the same conclusion: SRT is highly likely to be cost-effective. However, given that SRT was not cost-saving for the NHS over 12 months, future implementation research is needed to assess incentives for practices to implement SRT, as well as capacity considerations in relation to nurse delivery.

Strengths and limitations

The HABIT trial is the largest trial of SRT to date and one of the largest trials of psychological treatment for insomnia, yielding precise estimates of effect. It is the only trial to perform cost-effective analysis over a 12-month follow-up period. We conducted the trial across multiple general practices, across different regions of England, and trained nurses without formal experience of sleep intervention or psychological therapy to effectively deliver brief SRT with high levels of fidelity. This supports the generalisability of our intervention, while the brief training and delivery model speaks to scalability. We initially sought to only train practice nurses but due to availability issues at some practices we also trained additional research nurses to deliver treatment; however, they represented a minority (22.5%), and none of them had prior experience delivering sleep or behavioural treatment.

Retention was 85% overall at 6 months and 79% at 12 months, which is higher than previous primary care studies in the UK19,32 and broadly consistent with CBT-I studies over shorter follow-up periods. 72 Participants in the treatment group were less likely to complete the primary outcome at all time points. We attribute this difference to the greater demands placed on participants in the SRT arm relative to SH with respect to scheduling of treatment sessions, recording of sleep diaries during the 4-week intervention phase, and (for some) the challenge and difficulties of following SRT instructions. Sensitivity analyses involving multiple imputation and covarying for baseline predictors of missingness yielded similar findings to the primary analysis. Indeed, even under conservative assumptions (i.e. models assuming high score differences between those with missing and non-missing ISI outcome), the conclusion remained the same. Although the pandemic affected the last 12 months of the trial, treatment adaptation was required for just 13 participants, and exploratory analysis of the 6-month primary outcome revealed no difference for pre versus during the pandemic. The pandemic also adversely affected our ability to collect data on sleep diary parameters, medication use, and actigraphy-defined sleep, and thus such analyses should be interpreted with caution given the low levels of outcome completion.

Our sample reflects the clinical reality of insomnia in that the majority of participants were female, had experienced insomnia for a long time (approximately 10 years), and had a range of comorbid conditions (89% had at least one comorbidity and 51% had three or more). Moreover, the majority had consulted their GP in relation to insomnia and 25% were taking prescribed sleep medication at baseline. However, our sample and results may not generalise to the entire UK insomnia population because participants tended to be well-educated (50% had a university degree), were more likely to be from a white ethnic background (97% of the sample), and live in areas with low levels of deprivation. These sample characteristics may, in part, be driven by greater than anticipated recruitment in Oxfordshire (which was unexpected but necessary to compensate for under-recruitment). There was, however, no evidence that the treatment effect was lower in people from more-deprived circumstances, but the analyses lacked power to detect such moderation. It was not possible to conduct such moderation analyses by ethnic group. Future trials should be informed by INCLUDE guidance and roadmap100 in order to improve representation of under-served groups and increase diversity of recruited participants.

Participants were not blind to treatment group and the primary outcome was self-reported insomnia severity; therefore, there is potential for bias in reporting. However, we did not reveal the hypothesis to participants (the study was set up as a test of two different sleep improvement programmes) and nurses were not involved in the collection of trial outcomes. We therefore believe that bias is unlikely to explain the results. In support of this, previous work has tested, and demonstrated superiority of, SRT against an active control condition matched for therapist time, support and implementation of behavioural sleep advice. 24,25 A related point is that while SRT clearly out-performed SH, the SH group showed a reduction in ISI scores of approximately 3.5 points from baseline to 6 months. It is not clear what explains this reduction, but it may reflect regression to the mean, the natural course of insomnia over time, the effect of taking part in a study and/or the effect of SH.

Our approach to screening was automated and based on responses to questionnaires in order to assess for and exclude conditions that may not be suitable for SRT. We took this approach because it simulates a potentially scalable method that could be implemented in clinical practice, since primary care staff are not experts in sleep medicine. Nevertheless, without clinical interview or polysomnographic evaluation it is possible that some patients in the trial had undiagnosed sleep disorders, which plausibly could lead to a marginal dilution of the treatment effect.

Implications for health care

Our trial shows that nurses can be trained to deliver a focused and manualised behavioural insomnia treatment, leading to patient benefit, and without safety concerns. Moreover, the intervention is very likely to be cost-effective. Nurse-delivered SRT could therefore become part of primary care management of insomnia. At present, patients are typically provided with SH advice or sedative medication. NICE guidelines recommend that patients with insomnia are offered CBT-I as the first-line treatment, but there is limited access to psychological treatment for insomnia, with the exception of a few specialist clinics or services, or digital CBT implementation projects. The European Academy of CBT for insomnia articulates a vision ‘to develop services in such a way that CBT-I becomes available at a scale equivalent to medication’ and emphasises GP intervention and digital CBT. 101 There are practice nurses in every GP surgery (approximately 23,000 practice nurses across England) who may have the capacity to support people with insomnia using behavioural therapy, consistent with other clinical activities like weight management and smoking cessation. This is likely to result in a shift of consultation from GPs to practice nurses. Nurses and practice managers in the HABIT trial considered it to be feasible and had additional suggestions for implementation, including group sessions and enhanced flexibility in scheduling appointments. Nurse-delivered treatment could complement initiatives to increase access to digital therapies and cater for those who prefer face-to-face contact with a health professional – indeed qualitative interviews emphasised the importance of face-to-face sessions for SRT engagement. Those who do not achieve sufficient response to nurse treatment could then be reviewed by the GP and, if appropriate, referred to a specialist in sleep.

It is also possible that this treatment with its brief training and delivery model could be incorporated into the Improving Access to Psychological Therapies (IAPT) service in England. Most people with depression and anxiety, the main conditions treated within IAPT, experience insomnia symptoms and our data show improvement in PHQ-9 and SF-36 MCS scores. Thus, our sleep treatment package may improve outcomes for many patients in IAPT programmes. Finally, beyond UK health care, brief nurse-delivered behavioural treatment could widen access to evidence-based intervention in developing countries where there are limited dedicated mental health provision and barriers to digital engagement.

Recommendations for future research

Below we summarise specific research areas that should be followed up in future studies to build on the findings of the HABIT trial:

1. Formally investigate the integration of nurse-delivered SRT into the insomnia management pathway in primary care, for example as part of a stepped-care framework.

2. Assess generalisability of results across diverse primary care patients with insomnia.

3. Investigate additional methods to support patient engagement with treatment.

4. From a health economics perspective, investigate practice incentives for adopting SRT, including practice nurse capacity.

5. Investigate the effects of nurse-delivered SRT in specific subgroups, for example long-term hypnotic users, people with mental health problems, those presenting with insomnia for the first time.

Conclusions

Brief nurse-delivered SRT in primary care is clinically effective for insomnia disorder, safe, and likely to be cost-effective. SRT could become part of a stepped care approach to insomnia treatment, helping to facilitate the implementation of NICE guidelines and increase access to evidence-based intervention.

Contributions of authors

Simon D Kyle (https://orcid.org/0000-0002-9581-5311) (Professor of Clinical Neurosciences) was Chief Investigator, developed the original idea for the study and funding application with co-investigators, oversaw the delivery of the trial, led intervention design, training and delivery and led the writing of the final report.

Peter Bower (https://orcid.org/0000-0001-9558-3349) (Professor of Health Services Research) was a co-investigator on the funding application, designed the study, was responsible for its conduct and contributed to the writing of the report.

Ly-Mee Yu (https://orcid.org/0000-0003-0331-7364) (Associate Professor) was a co-investigator on the funding application, designed the study, was responsible for its conduct, led statistical analysis and contributed to the writing of the report.

Aloysius Niroshan Siriwardena (https://orcid.org/0000-0003-2484-8201) (Professor of Primary and Pre-Hospital Health Care) was a co-investigator on the funding application, designed the study, was responsible for its conduct, led the process evaluation and contributed to the writing of the report.

Yaling Yang (https://orcid.org/0000-0002-9529-1685) (Senior Researcher in Health Economics) performed the health economic evaluation and contributed to the writing of the report.

Stavros Petrou (https://orcid.org/0000-0003-3121-6050) (Professor of Health Economics) provided oversight of the health economic evaluation and contributed to the writing of the report.

Emma Ogburn (https://orcid.org/0000-0001-7643-572X) (CTU Director of Operations) was a co-investigator on the funding application, designed the study, was responsible for its conduct and contributed to the writing of the report.

Nargis Begum (https://orcid.org/0000-0002-8628-0319) (Clinical Trial Manager) was the trial manager, contributed to data collection and contributed to the writing and formatting of the report.

Leonie Maurer (https://orcid.org/0000-0001-7335-2320) (Post-Doctoral Research Associate) contributed to data collection, led actigraphy analysis, and contributed to the writing and formatting of the report.

Barbara Robinson (https://orcid.org/0000-0002-1721-7682) (Clinical Trial Facilitator) contributed to data collection and the writing and formatting of the report.

Caroline Gardner (https://orcid.org/0000-0003-0487-3979) (Post-Doctoral Research Associate) contributed to data collection and the writing and formatting of the report.

Stephanie Armstrong (https://orcid.org/0000-0002-2599-4844) (Senior Lecturer in Health Quality Improvement) contributed to data collection and analysis as part of the process evaluation, and contributed to the writing and formatting of the report.

Julie Pattinson (https://orcid.org/0000-0002-9824-3400) (Post-Doctoral Research Associate) contributed to data collection and the process evaluation, and contributed to the writing and formatting of the report.

Colin A Espie (https://orcid.org/0000-0002-1294-8734) (Professor of Sleep Medicine) was a co-investigator on the funding application, designed the study, was responsible for its conduct and contributed to the writing of the report.

Paul Aveyard (https://orcid.org/0000-0002-1802-4217) (Professor of Behavioural Medicine) was a co-investigator on the funding application, designed the study, was responsible for its conduct, was medical lead for the trial and contributed to the writing of the report.

Acknowledgements

We would like to thank all participants, nurses and practices who took part in the trial. We would like to acknowledge the research teams and administrators at sites in Thames Valley, Manchester and Lincoln, and the NIHR CRN. We would like to thank the TSC and DMEC, and our PPI Advisors (Danny Axford and Amanda Brewster) for supporting the trial.

Patient data statement

This work uses data provided by patients and collected by the NHS as part of their care and support. Using patient data is vital to improve health and care for everyone. There is huge potential to make better use of information from people’s patient records, to understand more about disease, develop new treatments, monitor safety and plan NHS services. Patient data should be kept safe and secure, to protect everyone’s privacy, and it’s important that there are safeguards to make sure that they are stored and used responsibly. Everyone should be able to find out about how patient data are used. #datasaveslives You can find out more about the background to this citation here: https://understandingpatientdata.org.uk/data-citation.

Data-sharing statement

All data requests should be submitted to the corresponding author for consideration. Access to anonymised data may be granted following review.

Ethics statement

The trial received both Health Research Authority approval (IRAS: 238138) and ethical approval (Yorkshire and the Humber – Bradford Leeds REC, reference: 18/YH/0153).

Information governance statement

The University of Oxford is committed to handling all personal information in line with the UK Data Protection Act (2018) and the General Data Protection Regulation (EU GDPR) 2016/679. Under the Data Protection legislation, the University of Oxford is the Data Controller, and you can find out more about how we handle personal data, including how to exercise your individual rights, and the contact details for our Data Protection Officer here (https://compliance.admin.ox.ac.uk/individual-rights).

Disclosure of interests

Full disclosure of interests: Completed ICMJE forms for all authors, including all related interests, are available in the toolkit on the NIHR Journals Library report publication page at https://doi.org/10.3310/RJYT4275.

Primary conflicts of interest: Simon D Kyle declares research funding from NIHR HTA (16/84/01 and 12/87/61), EME (NIHR131789) and Oxford Biomedical Research Centre and the Oxford Health Biomedical Research Centre, and non-financial support from Big Health Ltd. in the form of no-cost access to the digital sleep improvement programme, Sleepio, for use in clinical research (outside the submitted work). Paul Aveyard is NIHR Senior Investigator and declares research funding from NIHR HTA, NIHR Oxford Biomedical Research Centre, and NIHR Oxford and Thames Valley Applied Research Collaboration. Aloysius Niroshan Siriwardena declares research funding from Wellcome trust and NIHR HTA, RFPB and HS&DR. Ly-Mee Yu declares research funding from NIHR HTA. Peter Bower declares research funding from NIHR HTA. Leonie Maurer declares funding from NIHR Oxford BRC and consultancy fees from Mementor DE GmbH, outside the submitted work. Colin A Espie declares research funding from NIHR HTA, EME and Oxford Biomedical Research Centre, and is co-founder of and shareholder in Big Health Ltd., a company which specialises in the digital delivery of cognitive–behavioural therapy for sleep improvement (the Sleepio programme), outside the submitted work. All other authors declare no competing interests. Yaling Yang declares research funding from NIHR HTA, NIHR MIC and NIHR ARC Oxford and Thames Valley. Stavros Petrou receives support as a UK National Institute for Health and Care Research (NIHR) Senior Investigator (NF-SI-0616-10103) and from the NIHR Applied Research Collaboration Oxford and Thames Valley.

Disclaimers

This article presents independent research funded by the National Institute for Health and Care Research (NIHR). The views and opinions expressed by authors in this publication are those of the authors and do not necessarily reflect those of the NHS, the NIHR, the HTA programme or the Department of Health and Social Care. If there are verbatim quotations included in this publication the views and opinions expressed by the interviewees are those of the interviewees and do not necessarily reflect those of the authors, those of the NHS, the NIHR, the HTA programme or the Department of Health and Social Care.

Pattern mixture model results

Assumptions of the missing data mechanism were explored by imputing missing ISI outcome values that were up to five points either side of the observed average, both overall and in the SRT and SH arms separately. The results are displayed in Figure 21. If all participants with a missing ISI outcome at 6 months had an average ISI total score of 5 higher or 5 lower than those who were not missing, the estimated treatment effect and 95% confidence interval would still not include zero. If all participants with a missing 6-month ISI total score in the SRT group had an average ISI total score of 5 points higher than those who were not missing, and if all participants with a missing ISI total score in the SH group had an average ISI total score of 5 points lower than those who were not missing, the treatment effect and 95% CI would still not include zero.

FIGURE 21.

Results from pattern mixture model for the primary outcome at 6 months.

Assuming plausible arm-specific differences

We used the approach by White et al. 2011102 to carry out sensitivity analyses to investigate informative missingness of insomnia severity outcome data at 6 months. The following assumptions of differences between responders and non-responder were carried out:

• when the proportions of missing ISI score at 6 months are assumed to be the same in both arms (i.e. both arms equally), assume the mean unobserved responses for ISI score at 6 months could be as much as 75% more or 50% less (i.e. −50%) than the mean of observed responses;

• when the data are assumed to be informatively missing only in the SRT arm, assume the mean of unobserved responses for ISI score at 6 months could be as much as 50% more or 50% less (i.e. −50%) than the mean of observed responses;

• when the data are assumed to be informatively missing only in the SH arm, assume the mean of unobserved responses for ISI score at 6 months could be as much as 50% more or 50% less (i.e. −50%) than the mean of observed responses;

• additionally, more moderate sensitivity analyses include:

  • data are informatively missing in both arms, assume 50%

  • data are informatively missing in the SRT arm, assume as much as 25% more

  • data are informatively missing in SH arm, assume as much as 25% more.

Table 34 shows results when we assume plausible arm-specific differences of missing ISI score at 6 months between responders and non-responders. The results indicate that even with asymmetrical differences between responders and non-responders conclusions remain similar to the primary analysis.