AESOPS: a randomised controlled trial of the clinical effectiveness and cost-effectiveness of opportunistic screening and stepped care interventions for older hazardous alcohol users in primary care.

Article history paragraph text

The research reported in this issue of the journal was funded by the HTA programme as project number 06/304/142. The contractual start date was in April 2007. The draft report began editorial review in April 2012 and was accepted for publication in October 2012. 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’ report 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 report.

Copyright statement

© Queen's Printer and Controller of HMSO 2013. This work was produced by Watson et al. under the terms of a commissioning contract issued by the Secretary of State for Health. This issue may be freely reproduced for the purposes of private research and study and extracts (or indeed, the full report) may be included in professional journals provided that suitable acknowledgement is made and the reproduction is not associated with any form of advertising. Applications for commercial reproduction should be addressed to: NIHR Journals Library, National Institute for Health Research, Evaluation, Trials and Studies Coordinating Centre, Alpha House, University of Southampton Science Park, Southampton SO16 7NS, UK.

Research objectives

• To evaluate the clinical effectiveness and cost effectiveness of stepped care interventions for older hazardous alcohol users in primary care.

• To screen 4170 primary care attendees aged ≥ 55 years for hazardous alcohol use using the AUDIT questionnaire.

• To evaluate the acceptability and validity of opportunistically screening for hazardous alcohol use in older primary care attendees.

• To estimate the prevalence of alcohol use disorders in an older primary care population.

• To study the process of therapy as delivered by both practice nurses and trained therapists.

• To randomise 500 hazardous alcohol users, with equal probability, to either a minimal intervention or stepped care.

• To conduct 6- and 12-month follow-up on at least 70% of those randomised to assess alcohol consumption, alcohol-related problems, quality of life and service utilisation.

Primary hypothesis (stated as a null hypothesis)

• Stepped care interventions for older hazardous alcohol users are no more effective at reducing alcohol consumption than a minimal intervention 12 months after randomisation.

Secondary hypotheses (stated as a null hypothesis)

• Stepped care is no more cost-effective than minimal intervention 12 months after randomisation.

• Stepped care will not reduce alcohol-related problems in comparison with minimal intervention 12 months after randomisation.

• Stepped care will not increase health-related quality of life (HRQoL) compared with minimal intervention 12 months after randomisation.

Trial design

The Alcohol: Evaluating Stepped care in Older Populations Study (AESOPS) was a pragmatic, multicentre, two-armed, randomised controlled, open trial with equal randomisation. Participants aged ≥ 5 years who scored ≥ 8 using the AUDIT and consented to participate were randomised (1 : 1) to receive either:

• minimal intervention consisting of a 5-minute brief advice intervention with the practice nurse or research nurse involving feedback of the results of the screening and discussion regarding the health consequences of continued hazardous alcohol consumption; or

• stepped care intervention consisting of three consecutive steps, in which progression between steps is dependent upon the outcome of each previous step.

The study protocol can be seen in Appendix 1.

Sample size

At the time of development, there were no previous studies of stepped care interventions for older alcohol-using adults. The closest UK pragmatic randomised controlled trials (RCTs) include that by Wallace et al. 27 and STEPWICE,52 which reported effect size differences between stepped care and minimal interventions of 0.36 and 0.27 respectively. Similar effect size differences were reported in studies from the USA. 35,53,54 There is evidence that older populations respond to brief psychosocial interventions for alcohol use as well as, or even better than, general populations. 38,55 Assuming a conservative effect size difference between stepped care and minimal intervention of the order of 0.3 would require a sample size of 175 participants in each of the two randomised groups, using power at 80% and a 5% significance level.

Our previous experience in conducting RCTs in the fields of substance use, alcohol-using populations44,52 and elderly populations indicated that, with assiduous follow-up regimes, loss to follow-up at 12 months would be in the order of 20%. Evidence also exists that older populations are more compliant with treatment regimes and follow-up protocols than younger populations. 56 Taking these factors into account, we erred on the side of caution and allowed a loss to follow-up of 30%, requiring 500 participants to be randomised (250 in each group). Previous alcohol use screening and intervention studies conducted in UK health-care settings57 suggest that 80% of those screened positive tend to be eligible and 75% of those eligible tend to consent to randomisation. This meant that the study required 834 screen-positives, of whom we predicted 500 would be eligible and consent to randomisation.

Approvals obtained

North West Research Ethics Committee approved the study on 11 April 2007.

The details of multicentre research ethics committee, local research ethics committee and Research and Development Department approvals are provided in Appendix 2.

The trial was assigned the International Standard Randomised Controlled Trial Number (ISRCTN) of ISRCTN52557360; National Research Register number N0484190633 and United Kingdom Clinical Research Network ID 3796.

Trial sites

The study was conducted in eight UK sites with 55 general practices set up to participate. These sites and practices were recruited throughout the study and represent a range of small and large practices, and urban and rural settings. The sites included were North Yorkshire and York; Hull and East Riding; Norfolk; Leeds; Fife; Kent; Tyneside; and County Durham. Details of the study sites and practices are provided in Appendix 3.

Participant eligibility

Inclusion and exclusion criteria were chosen to maintain a balance between ensuring the sample was representative of the primary care population and ensuring that the trial population was able to engage with both the interventions and follow-up.

Recruitment into the trial

All primary care attendees aged ≥ 55 years were given the opportunity to pick up a ‘screening pack’ from the practice waiting room or from the receptionist. The screening pack contained an information sheet (Appendix 4), a copy of the AUDIT questionnaire (Appendix 5) and a freepost return envelope. The AUDIT questionnaire contained a section asking for contact details to be provided if the patient was willing to help with the research; thereby, patients had the opportunity to complete the form anonymously. This envelope could either be posted back to the University of York (allowing for completion at home if preferred) or left in a postal box within the GP practice. Returned questionnaires were entered into a secure online database that collated the responses to all 10 questions on the AUDIT questionnaire. Patients who scored ≥ 8 on the AUDIT questionnaire, and had provided their contact details, were contacted by telephone and invited to attend an appointment with the practice/research nurse, ideally within the following 7 days. At that point they had the opportunity to ask any questions. At the appointment, the study was fully explained to the patients, their eligibility to participate was ascertained and they were given an opportunity to ask any further questions. If interested and willing, they were then asked to give written informed consent.

During the study recruitment phase, a change in screening method was brought in (detailed in Chapter 3). In addition to the opportunistic screening method, all potentially eligible participants received screening packs by mail from their general practice. This revised method was implemented in some of those practices already screening opportunistically and in all new practices brought on board after the change was implemented.

Randomisation

Participants were randomised equally between the two trial arms: minimal intervention and stepped care intervention. Randomisation was carried out using random permuted blocks, stratified by site (North Yorkshire and York; Hull and East Riding; Norfolk; Leeds; Fife; Kent; Tyneside; or County Durham). To maintain allocation concealment, the generation of the randomisation sequence and subsequent treatment allocation were performed by an independent, secure, remote, telephone randomisation service based at the University of York. The computerised randomisation system was checked periodically during the trial following standard operating procedures. Owing to the nature of the intervention and the pragmatic aim of the evaluation, treatment allocation, once determined, was not concealed from the participant or the professional delivering the intervention.

Trial interventions

Participants were randomised to receive either:

• minimal intervention: a 5-minute brief advice intervention with the practice nurse or research nurse involving feedback of the results of the screening and discussion regarding the health consequences of continued hazardous alcohol consumption; or

• stepped care intervention: consisting of three consecutive steps, in which progression between steps is dependent upon the outcome of each previous step.

Measurement and verification of primary measure

The primary outcome measure was average drinks per day (ADD) at 12 months post randomisation, where a standard drink equates to 8 g of ethanol.

Measurement and verification of secondary outcomes

Collection of resource-use data

At recruitment (baseline) and 6 and 12 months after randomisation, participants were asked to complete a questionnaire on health and social care resource use during the previous 6 months (Appendix 6). The questionnaire was designed for participant completion and was returned to the trial office using a prepaid reply envelope. Participants indicated how many times in the previous 6 months they had used health services, for example if they had seen a GP or nurse or received hospital care. In addition, they were asked about contact with the police and criminal justice system. The collection of self-reported resource-use data was continued until the patient had been in the study for 12 months or until the patient withdrew from follow-up, or fully withdrew from the study.

Quality assurance of treatment delivery

Participants were asked to provide consent to have all treatment sessions recorded. A 30% sample was randomly selected, stratified by therapist, site and treatment (minimal and stepped care). Recordings were rated by an independent rater and assessed for quality of delivery and compliance with treatment protocols. A proportion of the recordings were double rated for quality assurances and calibration.

Adverse events

There were no anticipated risks in relation to either treatment arm and there is no documented evidence of adverse events arising as a result of either minimal intervention or stepped care intervention, but a mechanism for recording these was in place in case any arose.

Non-trial participants

Patients who had returned their screening forms and entered their contact details indicating willingness to be approached, but were subsequently found not to be eligible based on their AUDIT score (i.e. they scored < 8), were sent a letter informing them of the outcome of the screening. In addition, a ‘non-participant’ questionnaire identical to the study baseline questionnaire was included and patients were asked to complete this if they so wished and return it anonymously (Appendix 6).

Clinical analyses methods

The objective of the clinical analyses was to compare the clinical effectiveness and cost-effectiveness of stepped care interventions for older hazardous alcohol users in primary care.

Outcomes

Economic analysis

Economic evaluation of health interventions is a tool used to assist decision-makers in prioritising and allocating resources in the health-care sector, by assessing the value for money (cost-effectiveness) of alternative interventions. 70

The aim of the economic evaluation was to assess the cost-effectiveness of a stepped care intervention compared with minimal intervention in the treatment of older hazardous alcohol users in primary care.

The first stage of the economic analysis was to calculate the cost of delivering the trial treatments. Opportunistic screening costs were estimated using the actual costs of screening associated with the study. The costs of delivering the minimal intervention and the first two tiers of stepped care were based on actual patient contact time from timesheets maintained by practice or research nurses and therapists. The costs of the minimal intervention and the first two tiers of the stepped care programme were based on information gathered on patient contact with the primary care and specialist services during the trial.

The costs of the trial interventions were calculated using local costs of specialist services and included an allowance for the training and supervision costs, using methods developed for the UKATT trial. 71 Utilisation of more specialist services was recorded, including the type of intervention, and costs were applied from previous research trials and a recent Department of Health-funded research project based on a range of specialist providers and intervention types. 72 The incremental cost-effectiveness of stepped care compared with the minimal intervention was assessed from both a health and a personal social services perspective following National Institute for Health and Care Excellence (NICE) guidance73 and a wider public sector resource perspective. 73 Utilisation of alcohol services outside the trial protocol, along with all other public sector services, including health, social welfare and contact with criminal justice agencies, was assessed from questionnaires administered at baseline and 6 and 12 months. Units of resource use recorded were multiplied by national sources of unit costs71,74 in order to provide generalisable results.

The economic analysis tested the hypothesis that stepped care is more cost-effective than the minimal intervention, using a cost–utility framework. Utility values were derived from the EQ-5D60 and were then used with population values and the quality-adjusted life-year (QALY) change calculated using the area under the curve method. 75 Incremental cost-effectiveness analysis combined the costs of the interventions, as detailed above, with the QALY changes, using the cost in the intervention group over and above the control, divided by the incremental QALYs in the intervention group over and above the control. The non-parametric bootstrap resampling technique was used to test the sensitivity of the calculated incremental cost-effectiveness ratios (ICERs) and cost-acceptability curves estimated to demonstrate different threshold values for a QALY. 76 This would show the probability that stepped care was the preferred treatment option at different values for the decision-maker's willingness to pay for a QALY.

The effects of the GP practice were analysed using a multilevel model programmed in MLwiN (MLwiN, Centre for Multilevel Modelling, Bristol, UK). A net benefit framework was used, estimating the benefit of treatment by multiplying QALY changes by a £30,000-per-QALY value net of treatment cost. This estimated a net benefit of treatment for each patient in the trial. The multilevel model tested the proportion of the variation in the net benefit of treatment attributable to the practice to investigate the effect of the treatment location.

Outcome measures

In the original protocol the intention was to ascertain a diagnosis of alcohol use disorder using the Short Form-Composite International Diagnostic Interview (SF-CIDI). It was decided to replace this instrument with the AUDIT, with a score of ≥ 16 indicative of higher-risk alcohol use and possible alcohol dependence. The AUDIT has established sensitivity and specificity for the identification of at-risk alcohol use, inclusive of higher risk and possibly dependent alcohol use, and using this instrument reduced the response burden on participants. In addition, the primary outcome measure (ADD) was to be measured using a timeline follow-back method. This method would have involved a 20- to 30-minute interview with a trained researcher at each of the outcome assessment points. We replaced this with a validated, reliable self-complete instrument: the extended AUDIT-C. Evidence exists that the timeline follow-back method acts as a brief intervention and as such may act to reduce the observed differences between allocated groups. 77 Using the extended AUDIT-C reduced this measurement effect, as well as the response burden on participants. The original protocol had outlined our plan to conduct follow-ups face to face at 6 and 12 months post randomisation. As the primary outcome measure was replaced with a self-completed instrument it was decided to replace this follow-up method with postal follow-ups at 6 and 12 months post randomisation, meaning that the participants did not have to return to the practice for any follow-up assessments.

Recruitment period

The original protocol planned to recruit 500 participants over an 18-month period with all participants being followed up for 12 months. As the study progressed, delays to practice initiations meant that the study had fallen behind schedule, with the first patient not recruited until April 2008. The original end date for recruitment was 31 April 2009. In addition, the recruitment rate was found to be under target as a result of prevalence and uptake rates being lower than anticipated. This led us to apply to the funder in November 2008 for an 18-month extension to the recruitment period. The original sample size remained unchanged. The funders elected instead to track recruitment through monthly reports until the end of January 2010, during which time it would become clearer whether or not the target was achievable within an acceptable timescale. New sites and practices were brought on board (Appendix 3 details start dates of trial sites) and, following a successful increase in recruitment, in February 2010 an extension was approved allowing recruitment to continue until the end of October 2010, with the 12-month follow-up ceasing by the end of November 2011.

Trial recruitment

Eight sites participated in the study from across the UK. These were North Yorkshire and York; Hull and East Riding; Norfolk; Leeds; Fife; Kent; Tyneside; and County Durham. The number of participants recruited per site ranged from 3 to 209. Within these sites, 55 GP practices were set up, but only 53 commenced screening patients. Participants were recruited from 51 of the 53 practices and the number of participants recruited per practice ranged from 1 to 54.

Screening commenced in January 2008 and continued through to October 2010. Approximately 78,000 screening questionnaires were distributed, with over 60,000 of these by mail-out. Twenty-five practices used opportunistic screening only, 28 used mail-out only and six switched from opportunistic screening to mail-out (as detailed in Appendix 3). The majority of screening questionnaires returned were from the Tyneside and Leeds sites. The first participant was recruited in April 2008 and recruitment ceased at the end of October 2010. The participant follow-up period ended in November 2011 after which point the study ended.

In total, 21,545 completed screening forms were returned. Sixteen had insufficient information to score the AUDIT. Of the remainder, 1625 were AUDIT positive (scored ≥ 8 on the AUDIT) (1625/21,529 = 7.5%). This indicates that 7.5% of the population screened were considered hazardous or harmful drinkers, a rate much lower than anticipated (15% to 25%). The proportion of hazardous or harmful drinkers ranged from 6.6% to 10.4% across the sites (Table 1).

In total, there were 949 patients who were AUDIT positive and provided contact details; they had an average AUDIT score of 12.10 [standard deviation (SD) 5.65], which was higher than for those who were AUDIT positive but did not provide contact details (Table 2).

The percentage of eligible patients (i.e. AUDIT positive with contact details provided) who were deemed fully eligible [928/1626 = 57% (i.e. 949 AUDIT positive, but 21 failed one or more of the other eligibility criteria)] and went on to be randomised was only 57% (529/928 = 57%).

Figure 1, the Consolidated Standards of Reporting Trials (CONSORT) flowchart, shows the progress of participants through the trial.

FIGURE 1.

The AESOPS CONSORT diagram.

Clinical data

In total, 529 participants were randomised: 266 to stepped care and 263 to minimal intervention. A baseline questionnaire was not received from seven participants following completion: three from the stepped care group and four from the minimal group.

The majority of participants were male (n = 425; 80%) and the average age was 63 years (range 55–85 years) (Table 3). A score of ≥ 20 on the AUDIT indicates possible alcohol dependence. Overall, 7.9% of those randomised obtained a score of ≥ 20 at screening. This was higher in the minimal group (9.5%) than in the stepped care group (6.4%). This is summarised in Table 4. The average AUDIT-C score was 8.3 (SD 2.2) and ADD was 3.39 (SD 2.2). The baseline characteristics are summarised by treatment group (Tables 5 and 6).

Comparing the trial participants with those screened, there were more males (80% compared with 45% in the screened population) and participants were slightly younger: 63 years compared with 68 years (Table 3).

Baseline data were collected on those who were willing to participate but were not eligible for the trial (non-participants) because they were AUDIT negative at screening. In order to compare the baseline characteristics of participants and non-participants, the AUDIT-C was also calculated for the screening sample. Comparing non-participants with trial participants, trial participants were younger and more likely to be male.

Analysis of clinical results

This portion of the report presents the results of the statistical models fitted to the data. It is arranged into three main sections. The first section presents the results of the modelling of the primary outcome: ADD at 12 months. The second section presents the results of the modelling of the secondary outcomes: ADD (derived from the extended AUDIT-C) at 6 months; alcohol-related problems assessed using the DPI at 6 and 12 months; extended AUDIT-C score at 6 and 12 months; and HRQoL at 6 and 12 months. The third section summarises the conclusions of the statistical analysis of the clinical outcomes.

Primary outcome

Overall, the mean ADD score in both groups decreased from baseline at both month 6 and month 12. At month 6 the stepped care group had a lower ADD but at month 12 the minimal intervention group had the lower ADD. This is summarised in Table 7. Figure 2 shows the mean ADD scores for the complete cases.

TABLE 7 - Summary of ADD

max., maximum; min., minimum.

Follow-up	Treatment arm
	Stepped care	Minimal	Total
Baseline
Valid n	263	255	518
Mean (SD)	3.38 (2.24)	3.41 (2.19)	3.39 (2.21)
Median (min., max.)	3.00 (0, 8.57)	3.00 (0, 8.57)	3.00 (0, 8.57)
Month 6
Valid n	236	229	465
Mean (SD)	2.45 (1.85)	2.81 (2.03)	2.63 (1.95)
Median (min., max.)	1.96 (0, 8.57)	2.25 (0, 8.57)	2.25 (0, 8.57)
Month 12
Valid n	228	228	456
Mean (SD)	2.56 (2.09)	2.49 (1.93)	2.53 (2.01)
Median (min., max.)	1.96 (0, 8.57)	2.25 (0, 8.57)	2.11 (0, 8.57)

FIGURE 2.

Average drinks per day (complete cases).

A mixed model was used to compare ADD between the two randomised groups. The baseline value of ADD was included as a covariate and a variable was also included for treatment group; these were included as fixed effects. To account for the variation due to GP practice, this was included as a random effect in the model. Expanding the model to a three-level model to include nurse/therapist resulted in a model that failed to converge, and so the final model used was a two-level mixed model with participants nested within GP practice.

The ADD had a skewed distribution; a transformation improved the model fit. A log-transformation was used in the final model so the dependent variable was Ln(ADD_M12 + 1) (M12 = month 12).

In total, 456 participants had a response at month 12; however, in seven, ADD value at baseline was missing, and so these participants were not included in the primary analysis. The GP random effect was not significant, indicating that transformed ADD did not vary significantly between centres. There were no significant differences in ADD between the treatment groups at month 12. The stepped care group had a marginally higher ADD than the minimal intervention group but not significantly so. The results of the analysis are seen in Table 8.

TABLE 8 - Estimates of ADD (Ln-transformed)

SE, standard error.

Follow-up	Stepped care estimate (SD) (n = 226)	Minimal estimate (SD)(n = 223)	Difference (95% CI)	p-value
Month 12	1.129 (0.037)	1.104 (0.037)	0.025 (−0.062 to 0.112)	0.575
Covariance parameter estimates			Estimate (SE)	p-value
Random GP effect			0.013 (0.009)	0.059
Measurement error			0.215 (0.015)	< 0.001

Transforming the data for the analysis was necessary because of the skewed distribution. As the transformation included the addition of 1, this meant that a back-transformation was more problematic; however, it was anticipated that this would not have a great influence on the back-transformed estimate. To verify this, an additional analysis, excluding those with an ADD of zero, was used to confirm the result. In order to summarise the results in a more meaningful way, the estimate of the difference was anti-logged. It was found that ADD at month 12 for the stepped care group was 1.025 [95% confidence interval (CI) 0.94 to 1.12] times that of the minimal group. The analysis excluding those with ADD of zero, carried out to check that the log(ADD + 1) produced a good approximation, produced very similar results, and so we concluded that these estimates were acceptable.

Analysis of secondary outcomes

In this section, the results of the secondary analysis are presented.

Summary

There was no evidence of a difference in ADD when comparing the stepped care group with the minimal intervention group at month 12.

There was no evidence of a difference in any of the secondary outcome measures (AUDIT score, alcohol-related problems and quality of life) at either month 6 or month 12.

Assessment of costs

A micro-costing approach was used to compute the costs of trial interventions. The estimation of costs involved three distinct phases: identifying the relevant resource-items; measuring the use of the identified resource-items; and assigning unit costs or prices to them.

Attendees at primary care aged ≥ 55 years were screened to determine if they were eligible for the trial interventions. Opportunistic screening costs were estimated from the actual resource use associated with the screening process, which consisted of an information letter, a copy of the AUDIT questionnaire and the time input of the practice/research nurse or practitioner who contacted screen-positive patients.

The costs of the minimal intervention and the first two tiers of the stepped care programme (step 1 and step 2) were based on information gathered on patient contact with the primary care and specialist services during the trial.

Participants in the control arm received a 5-minute discussion with a practice/research nurse about the health consequences of continued hazardous alcohol consumption, and a brief self-help leaflet. Therefore, the cost of minimal intervention included practice/research nurse time and material costs of the self-help leaflet.

The costs of stepped interventions were calculated using local costs of specialist services and included an allowance for training and supervision costs. For steps 1 and 2 of the intervention, therapists were invited to participate in training sessions to provide them with skills for delivering BCC (step 1) and MET (step 2). The cost component for training included the time that trainers and therapists spent in training and supervision, plus use of space and materials. The total cost for training in each stage was allocated to the number of sessions delivered for the trial.

Step 1 of the intervention included a 20-minute session of BCC by a practice/research nurse. Step 2 consisted of three 40-minute sessions of MET on a weekly basis delivered by a therapist such as an alcohol health worker, clinical nurse manager or drug and alcohol counsellor. The actual time therapists spent delivering each intervention session was recorded and used to compute actual intervention costs by multiplying by their individual salaries.

Four weeks after each step, participants were contacted by telephone by a practice/research nurse for a reassessment of their alcohol consumption. These costs were calculated based on an average 5 minutes of practice/research nurse time and the costs of the line rental.

Step 3 of the stepped care intervention was a referral to local specialist alcohol services to receive specialist intervention. The resource use of this step was not specified in the trial and could encompass a variety of intervention approaches; interventions in this step could expand beyond the time horizon of the trial and a standard cost of £811 per patient was assumed according to the literature. 81

Data on additional utilisation of health and social care and criminal justice services outside the trial protocol were collected from questionnaires administered at baseline, 6 months and 12 months. At each time point, participants were asked about their resource use over the previous 6 months. Units of resource use recorded were then multiplied by national sources of unit costs81 in order to provide generalisable results. Table 21 presents a summary of the categories of resource use together with their unit costs.

Assessment of outcome

The economic evaluation used QALYs as recommended by NICE as a measure of health benefit for their reference case. 73 QALYs were derived from utility scores measured by EQ-5D questionnaires at baseline and at 6-month and 12-month follow-up. The EQ-5D is a standardised instrument for use as a measure of health outcomes developed by the EuroQol Group. 60 The EQ-5D results were scored using the UK York time trade-off tariff obtained from a sample of around 3000 members of the general UK population. 83,84 Given the assumption that health status changes between measurements are smooth and gradual over time, utility scores were converted into QALYs using the area under the curve method. 85

To appropriately adjust potential imbalances and ensure comparability with the clinical analysis, multiple regression methods were applied to give the differential mean QALYs and the prediction of adjusted QALYs by controlling for baseline EQ-5D scores. 86,87

Assessment of cost-effectiveness

Incremental cost-effectiveness analysis was performed to combine the costs of the interventions with health outcomes. The mean difference in costs between the two trial groups was compared with mean difference in effectiveness to generate ICERs. 70

Here, E represents the change in effects (in this case measured QALYs), and C represents the costs of intervention, measured in monetary units, while subscripts ‘SC’ and ‘MI’ refer to stepped care and minimal intervention, respectively.

Handling uncertainty

Cost and QALY data are typically not normally distributed. Cost data are often highly right skewed because of a few cases that incur extremely high costs, while QALY data are normally left skewed because of the ceiling effect. 88–90 In this study, the non-parametric bootstrap technique was employed to explore the sensitivity of calculated ICERs. Bootstrapping is a resampling method that generates multiple replications of the statistic of interest (ICER) by sampling with replacement from the original data. 91 The bootstrap method is preferable for skewed data as it does not rely on parametric assumptions concerning the underlying distribution of data. 92,93

The results from the bootstrap resampling were used to plot cost-effectiveness planes (CEPs) and cost-effectiveness acceptability curves (CEACs) to show the decision uncertainty surrounding adoption decisions. The CEACs present the probability that stepped care is the preferred treatment option at different values for a decision-maker's willingness to pay (WTP) for a QALY. 94

Sensitivity analysis

Sensitivity analysis is an appropriate way to check on methodological uncertainty. In this study, sensitivity analysis was planned to vary assumptions about costing methods. It was found that the distributional problem that arose for cost data was mainly attributable to a few ‘extreme values’ in the distribution. Therefore, extreme values, defined as those deviating by five times the standard deviation, were excluded and the incremental cost-effectiveness analysis was repeated in the sensitivity analysis.

Results of economic analysis

A total of 21,546 primary care attendees aged ≥ 55 years were screened using the AUDIT questionnaire. A total of 529 hazardous alcohol drinkers were recruited to the trial and received either minimal or stepped care interventions.

The base-case cost-effectiveness analysis was based on 422 participants (212 in the stepped care group and 210 in the minimal intervention group) with both completed cost and outcome estimates for three different time points, i.e. baseline, 6-month and 12-month follow-up.

Outcomes

Mean EQ-5D scores are reported for both groups at the baseline, 6-month and 12-month post randomisations. Figure 3 presents the change of mean EQ-5D scores over time.

FIGURE 3.

Mean EQ-5D scores at baseline, 6 months and 12 months.

Figure 3 shows that, in both the intervention and control groups, mean EQ-5D scores at 6 months were lower than at baseline, while at the end of the 12-month follow-up, the scores increased and were higher than the baseline utilities. Changes in EQ-5D scores were transformed to estimate the QALY gains for each patient (Table 25). The mean unadjusted difference QALY gain over the 6 months from baseline was 0.4030 (SD 0.1026) in the stepped care group and 0.3843 (SD 0.1164) in the minimal intervention group. The corresponding QALY gains for the 12 months from baseline were 0.8067 (SD 0.2012) and 0.7717 (SD 0.2214), respectively.

TABLE 25 - Utility scores (EQ-5D index scores) and QALYs (n = 422)

Difference = utility for intervention group – utility for control group.

No adjustment.

Adjusted for baseline EQ-5D scores.

Outcome	Intervention group (SD) (n = 212)	Control group (SD) (n = 210)	Difference,a£ (95% CI)
Baseline EQ-5D scores	0.8066 (0.2204)	0.7767 (0.2507)	0.0299 (−0.0152 to 0.0751)
Six-month follow-up EQ-5D scores	0.8052 (0.2238)	0.7606 (0.2451)	0.0446 (−0.0003 to 0.0895)
Twelve-month follow-up EQ-5D scores	0.8098 (0.2304)	0.7891 (0.2257)	0.0207 (−0.0229 to 0.0644)
QALY (6 months)b	0.4030 (0.1026)	0.3843 (0.1164)	0.0186 (−0.0024 to 0.0396)
QALY (6 months)c	0.3966 (0.0394)	0.3908 (0.0394)	0.0058 (−0.0018 to 0.0133)
QALY (12 months)b	0.8067 (0.2012)	0.7717 (0.2214)	0.0350 (−0.0055 to 0.0755)
QALY (12 months)c	0.7951 (0.1054)	0.7834 (0.1054)	0.0117 (−0.0084 to 0.0318)

Similar to the cost calculation, there is imbalance occurring at the baseline in the mean EQ-5D scores in the two trial groups (Table 26). After adjusting QALYs for baseline EQ-5D, the results demonstrate that participants in the stepped care group had, on average, a slightly better quality of life than those in the minimal intervention group [difference in QALYs was 0.0058 (95% CI −0.0018 to 0.0133) at 6 months and 0.0117 (95% CI −0.0084 to 0.0318) at 12 months]. However, this difference was not statistically significant.

TABLE 26 - Results of incremental cost-effectiveness analysis (completed cases)

Outcome	6 months		12 months
	Stepped care (n = 212)	Minimal intervention (n = 210)	Stepped care (n = 212)	Minimal intervention (n = 210)
Cost (SD)	£488 (£826)	£482 (£826)	£895 (£2049)	£1089 (£2049)
QALY (SD)	0.3966 (0.0394)	0.3908 (0.0394)	0.7951 (0.1054)	0.7834 (0.1054)
ICER (95% CI)	–£1100 per QALY (−£85,991 to £95,546)		–£7997 per QALY (−£238,341 to £172,319)

Results of the cost-effectiveness analysis

Table 26 presents ICERs that combined the costs of interventions with health outcomes.

At the 6-month follow-up, both mean QALY gains and mean cost were greater in the stepped care group than in the minimal intervention group, generating an ICER of £1100 per QALY gained, while at the 12-month follow-up, minimal intervention is dominated by stepped care using the calculated average results. Stepped care participants receive more benefits (greater QALY gains) for less cost; however, none of the differences in costs and benefits between the two interventions was statistically significant. The bootstrap method was therefore employed to evaluate uncertainty surrounding cost-effectiveness estimates. Bootstrapping results were also used to generate incremental CEPs and CEACs to show uncertainty surrounding adoption decisions, shown in Figures 4 and 5.

FIGURE 4.

Cost-effectiveness plane (a), adjusted for baseline utility and costs, and cost-effectiveness acceptability curve (b), adjusted for baseline utility and costs, at 6 months (completed cases).

FIGURE 5.

Cost-effectiveness plane (a) and cost-effectiveness acceptability curve (b) at 12 months (completed cases).

For the 6-month follow-up period, the incremental cost-effectiveness plane (Figure 4) showed over half of the plots falling into the south-east quadrant, indicating that stepped care interventions were less costly and more effective. Given WTP thresholds of £20,000–30,000 per additional QALY gained, which is the decision-making threshold used by NICE, the probability that stepped care was more cost-effective is 81.3–86.4%.

Similarly, at the 12-month follow-up (Figure 5), the majority of plots in the cost-effectiveness scatter lay in the south-east quadrant and indicated that minimal intervention was dominated by stepped care interventions. The probability of stepped care being cost-effective was between 93.5–93.84% using NICE's threshold range of £20,000–30,000 per QALY gained.

The effects of the GP practice were analysed using a multilevel model programmed in MLwiN. Net monetary benefit was calculated using a WTP threshold of £30,000 per QALY. The analysis indicated that the net monetary benefit did not significantly differ by GP practice.

Results of the sensitivity analysis

Sensitivity analysis was carried out to check on costing methods in the economic evaluation. In total, 13 participants with extreme costs were excluded in the sensitivity analysis. The changes in costs were noticeable (Figure 6). Taking the 12-month resource use as an example, the mean cost for the control group fell from £1162 to £850, and the standard deviation dropped from £2636 to £1125. With the 409 cases left, the incremental cost-effectiveness analysis was repeated. The results are summarised in Table 27.

FIGURE 6.

Twelve-month health and social care resource use before and after removing extreme cases.

Twelve-month health and social care resource use before and after removing extreme cases.

Taking into account the sensitivity analysis, stepped care continues to demonstrate greater mean QALY gains; however, it is now more costly. The plots on the CEPs move upwards and to the left compared with base-case results. Now the adoption of the intervention relies only on the WTP threshold. Using the NICE threshold range of £20,000–30,000 per QALY, stepped care, with an incremental cost per QALY gained of £8496 at 6 months and £4224 at 12 months, is the more cost-effective option compared with minimal intervention.

Under the new set of ICERs, and using the £20,000–30,000 per QALY gained threshold, the probability that stepped care is more cost-effective ranges between 80% and 88% at 6 months and between 87% and 90% at 12 months (Figures 7 and 8).

FIGURE 7.

Cost-effectiveness plane and cost-effectiveness acceptability curve at 6 months (sensitivity analysis).

FIGURE 8.

Cost-effectiveness plane and cost-effectiveness acceptability curve at 12 months (sensitivity analysis).

Summary

The cost-effectiveness results indicated that the costs of delivering stepped care interventions were of the order of 20 times those of the minimal intervention [£46.63 (SD £146) vs £2.34 (SD £0)]. However, the overall cost per patient, taking into account health and social care resource use, was £488 (SD £826) in the stepped care group and £482 (SD £826) in the minimal intervention group at 6 months. The mean QALY gains were slightly greater in the stepped care group than in the minimal intervention group, with a mean difference of 0.0058 (95% CI −0.0018 to 0.0133), generating an ICER of £1100 per QALY gained. At month 12, participants in the stepped care group incurred fewer costs, with a mean difference of −£194 (95% CI −£585 to £198), and had gained 0.0117 more QALYs (95% CI −0.0084 to 0.0318) compared with the control group. From an economic perspective, therefore, the minimal intervention was dominated by stepped care.

The results, based on the resampled cost-effectiveness data from the bootstrapping, showed that the probability of stepped care being cost-effective was between 81% and 86% at the 6-month follow-up, and 93.5% and 93.8% at 12 months' follow-up given the NICE decision-making threshold range of £20,000–30,000 per QALY gained. This provides decision-makers with some useful evidence that stepped care interventions are more likely to achieve better value for money than minimal interventions. However, caution is required when interpreting the results given the uncertainty surrounding the estimates.

A sensitivity analysis that excluded extreme cases altered the average costs of interventions; the ICERs were £8496 per QALY at 6 months and £4224 per QALY at 12 months. The probability that stepped care is more cost-effective ranges between 80% and 88% at 6 months and between 87% and 90% at 12 months using the £20,000–30,000 per QALY gained WTP threshold.

Methods

Sampling

One hundred and sixty sessions of brief advice (minimal) and BCC (step 1) were selected for independent process rating (Figure 9). Only these two treatments were rated, as there were not enough MET sessions (step 2) to enable meaningful results to be obtained. The sample was stratified by site, practice/research nurse and treatment. Replacement sampling was used for eight inaudible recordings. In total, 79 sessions of brief advice and 81 sessions of BCC were rated. Nineteen per cent of these were double rated (i.e. scored by both the independent rater and supervisor): 11 sessions of brief advice and 20 of BCC.

FIGURE 9.

Flow diagram of process rating procedure.

Reliability of ratings

A sample of the recordings was rated by two raters. Inter-rater reliability of the individual frequency items of the summary scores was examined using the ICC two-way mixed-effects model (case 3). 67 For the four summary scores, the average of the two raters’ summary scores was plotted against the difference in their summary scores69 to make pairwise comparisons between raters (Figure 10).

FIGURE 10.

Bland–Altman plots.

The ICCs for the summary measures ranged from 0.64 to 0.81 (Table 36), which indicates acceptable levels of agreement. 67

TABLE 36 - Intraclass correlation coefficient analyses of the individual frequency items of the summary scores

Rating and raters	n	Mean rating (SD)	ICC (95% CI)
Task frequency
Rater 1	33	0.76 (0.45)	0.815 (0.624 to 0.908)
Rater 2	33	0.93 (0.50)
Task quality
Rater 1	33	0.51 (0.44)	0.670 (0.332 to 0.837)
Rater 2	33	0.82 (0.64)
Style frequency
Rater 1	33	2.30 (0.54)	0.736 (0.465 to 0.869)
Rater 2	33	2.41 (0.81)
Style quality
Rater 1	33	1.67 (0.60)	0.640 (0.271 to 0.822)
Rater 2	33	1.95 (0.85)

The Bland–Altman plots for each of the summary measures compare the two raters (Figure 10). A positive difference indicates that the second rater scores higher than the first rater. A negative difference indicates than the second rater scores lower than the first.

Summary

The scale identified significant differences between the 5- and 20-minute interventions, indicating that the two types of session were distinct. Validation of the rating showed an acceptable level of agreement between the raters. There were no significant differences in the rating scores between practice/research nurses with different levels of experience (specialist vs non-specialist practitioners).

Key findings

This study aimed to compare the effects of a minimal intervention (a 5-minute, brief advice with the practice/research nurse involving feedback of the results of the screening and discussion regarding the health consequences of continued hazardous alcohol consumption) with a stepped care intervention (progression to next step determined by reassessment of alcohol consumption after each previous step). The primary hypothesis was that a stepped care intervention reduced alcohol consumption in older hazardous alcohol users compared with a minimal intervention post randomisation. We found no evidence of a difference in the ADD after 12 months of older hazardous alcohol users when comparing the stepped care group with the minimal intervention group at month 12 [stepped care 1.129 (SD 0.037) vs minimal intervention 1.104 (SD 0.037)]. At month 6, the stepped care group had a lower ADD than the minimal interventions group, but not significantly so.

When adjusting for baseline scores and including GP as a random effect, there was no evidence of any differences in ADD at month 6, or AUDIT-C score or the DPI score at month 6 or month 12.

We investigated changes in HRQoL from baseline using the SF-12. 59 Our results showed that the stepped care group had both lower MCS and lower PCS than the minimal intervention group at months 6 and 12, although the differences were not significant at the 5% level. We cannot conclude that stepped care has any impact on HRQoL.

We evaluated whether or not stepped care was a more cost-effective treatment for the management of older alcohol users in primary care and the results revealed that, with longer follow-ups, stepped care generated greater cost savings (£194 at month 12 vs £6.38 at month 6) and greater QALY gains (0.0117 at month 12 vs 0.0058 at month 6).

The probability that stepped care was cost-effective was higher for the month 12 follow-up period (93.5–93.8%) than the month 6 follow-up (81–86%) under a conventional WTP threshold of £20,000–30,000 per QALY. This indicated that participants may benefit more from stepped care in the longer term with the reduction of alcohol-related health problems in the future. The analysis indicated that the net monetary benefit did not significantly differ by GP practice. A few ‘extreme values’ were present in the distribution (those deviating by five times the standard deviation) which were excluded, and the incremental cost effectiveness analysis was repeated in a sensitivity analysis. The sensitivity analysis altered the average costs of interventions; however, there was still over 80% certainty that stepped care is more cost-effective than minimal intervention months using the £20,000–30,000 per QALY gained threshold.

The health economic findings raise important issues when contrasted with the null clinical effectiveness findings and some further consideration of the reasons why this may occur is needed.

Firstly, in economic evaluation, an ICER combines the costs of the interventions with health outcomes. The statistic of interest is the ICER, which is estimated on the basis of four statistics from two samples: the costs of the control and intervention groups (C_C and C_I) and the effects of the control and intervention groups (E_C and E_I). This allows us to take advantage of the power to detect a difference in the joint cost-effectiveness outcome. In some cases, the power to detect a difference in this joint outcome exceeds the power to detect differences in either cost or effect alone. It is possible for a study to show no difference in clinical outcomes between interventions, but also to conclude that one intervention is more cost-effective than another, because that intervention costs less when the intervention's costs and subsequent service use are taken into account.

Secondly, the decision rule in an economic evaluation differs from traditional effect analysis. We make decisions to adopt a health technology by comparing the estimated cost-effectiveness ratio with a predefined standard or threshold value; for example, the decision-making threshold used by NICE is £20,000–30,000 per additional QALY gain. Whether or not an intervention is cost-effective varies when the decision threshold changes. Whereas in statistics an intervention is considered to be more effective if the p-value of the difference is lower than 0.05, this is not the case in an economic evaluation.

Thirdly, the traditional way of interpreting the CI may sometimes be interpreted in different ways in economic evaluation. For example, a negative ICER can arise as a result of two completely different situations. One scenario is that the intervention is more effective and less expensive. On the other side, the intervention may have a greater cost and a worse effect (cost-ineffective intervention). Therefore, we use CEACs to summarise the evidence in support of the intervention being cost-effective for all potential values of the decision rules. The CEAC presents much more information on uncertainty than it does on CIs in economic analysis, as it presents the probability that the intervention is more effective than the control at different values for a decision-maker's threshold, for example if willing to pay different values to gain one QALY.

It may be the case that the economic analysis indicates that with a far greater sample size a difference in effect of the interventions may become apparent. The sample analysed at the final outcome stage was greater than that estimated in the original sample size calculation and any small effect difference derived from a far larger sample would be unlikely to be a clinically important difference.

Consideration of possible explanations

The importance of the actual screening process itself cannot be excluded as having a possible impact on the alcohol consumption of some trial participants. Previous studies and reviews have reported possible reactivity to such assessments,77,102–105 although the exact effect is difficult to separate from the study interventions. The fact that the study involved the proactive opportunistic identification of people consuming alcohol at levels that may be detrimental to their health precluded the inclusion of a no-treatment control. Ethical considerations meant that the study compared two active interventions. The control was a minimally acceptable brief intervention and the provision of an information leaflet. The population identified using opportunistic screening exhibited lower levels of alcohol use and lower levels of alcohol-related problems than treatment-seeking populations and both groups reduced consumption over the 12 months. It may be the case that more intensive interventions in this population are no more effective than minimal interventions and similar results have been found in both systematic reviews and primary research. 28,34,106

The majority of participants engaged with both the minimal intervention and step 1 of the stepped care intervention and written comments on questionnaires were overwhelmingly positive in describing these. Of note was the fact that two-thirds of those assessed as eligible for referral to step 2 either cancelled or failed to attend. These findings are similar to other studies of stepped care for alcohol use in primary care,13 extended alcohol interventions for alcohol use in primary care106 and referrals for interventions in emergency departments. 107 It may be the case that extended multiple session interventions are not considered acceptable to a large proportion of the non-treatment-seeking population, many of whom are consuming alcohol at levels towards the lower end of the severity spectrum.

The use of the same practice/research nurse to deliver both the minimal intervention and step 1 of the stepped care intervention could have resulted in contamination due to the distinction between the interventions blurring and elements from each being found in the other. Verification of intervention fidelity not only ensures that internal validity of a study is maintained but also that external validity is enhanced. 108 This was achieved in AESOPS by each of the treatment sessions being recorded and also the fact that the PRS that was subsequently conducted did indeed identify significant differences between the 5- and 20-minute interventions, indicating that the two types of session were distinct. Therefore, in this study, having the same practice/research nurse deliver the minimal intervention and step 1 of the stepped care intervention is not considered to have affected the outcome.

In the early stages of the study, some problems had been encountered with participating practice nurses finding little time available to see study participants. As the recruitment methods changed, and an increase in potential participants identified was likely, the use of research/specialist practitioners was required (although the task of preparing and sending out the mailings did not involve the practice nurses). The possibility that these two groups (non-specialist and specialist) would be delivering the interventions differently was not proven by the PRS, where no significant differences in the rating scores between practice/research nurses with different levels of experience were found. We therefore do not consider this to have influenced the result in any way.

In the original study design we envisaged opportunistically screening patients as they attended the primary care centre and this being conducted by practice staff. In reality, difficulties in recruiting practices willing to engage in this process meant that the methods of recruitment had to be amended to include mail-out screening and the use of specialist study staff to intervene with the eligible population. This is an indication that opportunistic screening and the delivery of brief interventions embedded within primary care are not currently acceptable to primary care staff.

Comparison with previous research

Previous screening and intervention studies looking at alcohol use conducted in UK health-care settings52,57 suggested that 80% of those screened positive tend to be eligible and 75% of those eligible tend to consent to randomisation. In this study we found that only 57% of eligible patients consented to randomisation. Although still to be explored, it did not go unnoticed that a number of patients, either by written comment or by telephone, expressed the feeling that the time of the researchers would be better spent tackling binge-drinking and the perceived alcohol problems in the younger ages groups often highlighted in the media.

In addition, the prevalence of hazardous alcohol consumption, inclusive of harmful consumption and possible dependence, in those aged ≥ 55 years was estimated at 15% in the general population11 and greater, at 25%, in those attending primary care. 13 Screening results from this study found this to be only 7.5%.

The results of the clinical effectiveness aspects of the study appear to concur with recent research in the area. The population in question was an opportunistically identified population at the lower end of the alcohol use disorder spectrum. A recent systematic review of brief interventions in primary care28 found no additional benefit of more intensive versus briefer interventions. Primary research in the UK found no additional benefit of extensive brief lifestyle counselling over and above brief advice and the provision of an information leaflet for a general population identified opportunistically using AUDIT in primary care;106 in addition, a recent US study comparing minimal intervention with more intensive intervention for older alcohol users found that although alcohol use reduced in both groups there were no significant differences between the groups. 34 General population studies in primary care have established the benefits of brief interventions over and above no treatment controls28 and similar results have been reported for older people in primary care. 35,36

MEDLINE, EconLit, and NHS Economic Evaluation Database were searched for economic evaluations of alcohol treatments. Fewer than 30 full economic evaluations that compare both the costs and health consequences were found in literature. Only one trial (STEPWICE) was available that compared cost-effectiveness between stepped care and a 5-minute advice session. 51 The result of the cost-effectiveness analysis of the STEPWICE trial was very similar to AESOPS, but with a much smaller sample size (n = 112). Both studies found that stepped care was more likely to be cost-effective compared with minimal intervention using the NICE threshold range of £20,000–30,000 per QALY gained.

There are several difficulties when making direct comparisons between existing economic evaluations of alcohol treatments. Firstly, the definition of the interventions varies between studies. For example, ‘brief intervention’ was used as a common comparator in clinical trials109–112 but studies define brief intervention differently in terms of contact length, content and style. 113 Secondly, the evaluation of health consequences differs among studies. For instance, the most widely used outcome measurements were drinks per drinking day, binge-drinking episodes or heavy drinking, and percentage of days abstinent. Although some economic evaluations used QALYs as a health outcome measure following NICE's guidance71,114 none focuses on a similar population or interventions to the AESOPS study.

Strength and limitations of the study

Although we had originally estimated that we would recruit 500 participants from 15 GP practices in three sites over an 18-month period, it took twice this time and many more GP practices: 53 across eight sites. However, we did successfully recruit our target number of older hazardous alcohol users. Our finding of no evidence of a difference is not likely to be due to a lack of power.

As a result of the initial slow recruitment rate, a change in recruitment method was required, moving away from the original design of opportunistic screening in GP practice waiting rooms to the adoption of the more extensive method of mailing out forms to all patients aged ≥ 55 years on a participating GP practice register. This change, however, not only provided evidence of the limitations of using opportunistic screening at practice attendance as a recruitment method, but also allowed us to estimate a much more robust prevalence rate of hazardous alcohol consumption in this patient group, while also resulting in our recruitment target being met.

The lower than expected prevalence rate may be due to response bias, whereby those who are consuming alcohol at higher levels are less likely to respond to the AUDIT questionnaire and participate in the study. Yet participants were given an option to respond anonymously and those who did so had lower mean AUDIT scores than those who provided contact details, which may add further weight to the idea that the prevalence figure identified in the study is indicative of the true population prevalence rate. In addition, the study population was generalisable to the population of older alcohol users who were willing to be screened and to engage in an intervention to address their alcohol use.

In addition, there was a reluctance on the part of the primary care nurses to undertake these interventions, and reluctance on the part of the GPs to support their practice nurses in doing this. These issues individually, and together, made it difficult to pursue the protocol as designed without having to adapt in some way. This does, however, have important implications regarding the question of whether or not these sorts of interventions can be implemented in the primary care setting and it does not seem to be the case that practice nurses are enthusiastic about their delivery.

One limitation of this study was the low take-up by those referred to step 2 of the stepped care intervention. The precise reasons for this are unknown but a number of factors could be involved. These include possible unwillingness of participants to accept that their alcohol consumption was having a detrimental impact on their health, particularly if they consumed alcohol at lower levels of severity; unwillingness to reduce consumption any more than agreed in the initial session; or unwillingness or unavailability to attend more than one session. There may also be an issue with the time lag between identification of the problem and the intervention taking place, resulting in attendance being less likely.

Our previous experience in conducting RCTs in the fields of substance use (UKCBTMM), alcohol-using general adult populations (UKATT, STEPWICE) and elderly populations (RESPECT) indicate that, with rigorous follow-up regimes, loss to follow-up at 12 months would usually be in of the order of 20%. Taking these factors into account we had erred on the side of caution and allowed an attrition rate of 30%. In fact, in AESOPS the overall follow-up rate at month 12 was 87.5%, with 86.8% followed up in the stepped care group and 88.2% in the minimal intervention group.

In the cost-effectiveness analysis we made very conservative assumptions to ensure that the costs of the stepped care intervention were not underestimated. We did not take into account the possibility that interventions may prevent and reduce alcohol-related disease and injury, which may result in considerable cost savings, especially if these costs and expected impacts on health status were modelled over a longer time period.115 The absence of any criminal justice events within this study does suggest that the economic consequences of hazardous and harmful alcohol consumption could be different for older people, but this would need further investigation. It should also be noted that the training costs for practice nurses to deliver minimal intervention were not included in the control group. We assumed that they had already received training to deliver brief advice during their student nurse or early career training. If this part of the training cost was added into the control group, the minimal intervention would turn out to be even more costly compared with stepped care.

Generalisability of the results

The AESOPS recruited from eight sites and 53 GP practices across England and Scotland, including both urban and rural locations, in GP practices of varying sizes. With the population group within AESOPS, we are confident that these results are broadly generalisable to the population who would engage in screening and intervention for alcohol use problems in general practice.

Implications for health care

The evidence from this trial shows that there is no clinical advantage of opportunistic screening in addition to stepped care over opportunistic screening and minimal intervention in terms of the reduction in alcohol consumption at 12 months post intervention in hazardous alcohol users aged ≥ 55 years who score ≥ 8 on the AUDIT, but there is some evidence that it may be cost-effective.

Implications for research

The experience of conducting this research in primary care settings, the implication that extended interventions are not acceptable to participants or practice staff in the management of hazardous alcohol use and have no additional benefit over screening and minimal interventions, the potential to target those with more entrenched harmful or possible dependent alcohol use who are not seeking treatment and the finding that stepped care interventions appear to produce economic benefits have the following implications for future research:

• What factors facilitate or hinder the conduct of research in primary care settings?

• What is the effectiveness and cost-effectiveness of community-based screening and self-directed ultra-brief interventions for hazardous alcohol users compared with screening alone?

• What is the effectiveness and cost-effectiveness of MET for non-treatment-seeking harmful and possibly dependent alcohol users delivered in primary care?

• What are the longer-term clinical and economic impacts of stepped care interventions?

Collaborations and contributions of the authors

The AESOPS collaborators (current and past) are Martin Bland, Simon Coulton, Helen Crosby, Ben Cross, Veronica Dale, Colin Drummond, Christine Godfrey, Alan Hassey, Eileen Kaner, Jenny Lang, Ruth McGovern, Dorothy Newbury-Birch, Jo Orchard, Steve Parrott, Tom Phillips, Duncan Raistrick, Daphne Rumball, Gillian Tober, Valerie Wadsworth, Judith Watson and Qi Wu.

Simon Coulton was the chief investigator, chaired the Trial Management Group, edited and approved the final draft of the report.

Judith Watson was the trial manager.

Veronica Dale and Martin Bland designed the clinical analysis.

Veronica Dale conducted the clinical analyses and oversaw the process ratings analyses.

Qi Wu conducted the economic analyses.

Helen Crosby conducted the process ratings and analyses.

Gillian Tober developed the training, supervised the practice/research nurses and therapists and oversaw the process ratings.

Jenny Lang contributed to and co-ordinated recruitment to the trial in Leeds.

Dorothy Newbury-Birch and Ruth McGovern contributed to the study design and co-ordination and managed the Tyneside and County Durham recruitment to the trial.

Steve Parrott oversaw the conduct of the economic analyses.

Martin Bland oversaw the conduct of the analysis.

Colin Drummond, Christine Godfrey and Eileen Kaner contributed to the study design, conduct of the trial and the Trial Management Group.

Independent Steering Committee Members

Professor Oliver James – chairperson of Independent Steering Committee from August 2007 to end.

Professor Graham Dunn – member of Independent Steering Committee from August 2007 to end.

Professor Helen Smith – member of Independent Steering Committee from June 2009 to end.

Mrs Valerie Lipman – consumer representative and member of Independent Steering Committee from August 2007 to March 2008.

Disclaimer

This report presents independent research funded by the National Institute for Health 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, NETSCC, the HTA programme or the Department of Health.