The clinical and cost effectiveness of brief intervention for excessive alcohol consumption among people attending sexual health clinics: a randomised controlled trial (SHEAR)

Article history

The research reported in this issue of the journal was funded by the HTA programme as project number 09/91/04. The contractual start date was in April 2011. The draft report began editorial review in April 2013 and was accepted for publication in January 2014. 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.

Declared competing interests of authors

All authors have completed the unified competing interest form (available on request from the corresponding author). ALH has undertaken a consultancy for Lundbeck International Neuroscience Foundation, has applied for grants for support for brain scans from GlaxoSmithKline (GSK), pending from Lundbeck, and has received payment for lectures from the Lundbeck Institute, UK, Janssen, Pfizer and Servier. ALH was paid by Lundbeck for travel expenses to attend an international meeting. RJ has received payment (including travel expenses) for lectures for non-promotional educational tools devised for various producers of antiretroviral agents. Institutions for all authors have received funding from the National Institute for Health Research (NIHR) Health Technology Assessment (HTA) programme for other studies. MJC, RS, BB, SB, MD, JG, BL, MS, RT, PT and HW declare no other interests.

Copyright statement

© Queen’s Printer and Controller of HMSO 2014. This work was produced by Crawford 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.

Hypotheses

1. Brief intervention for those attending sexual health clinics and drinking excessively reduces mean weekly alcohol consumption over a 12-week period prior to the 6-month follow-up interview (i.e. weeks 13–24 after intervention).

2. Brief intervention for those attending sexual health clinics and drinking excessively reduces the likelihood of unprotected sexual intercourse over a 12-week period prior to the 6-month follow-up interview.

3. Brief intervention for those attending sexual health clinics and drinking excessively is more cost-effective than control treatment.

Changes to original protocol

Prior to the start of the study, but following trial registration, one of the clinics where we were due to recruit participants withdrew from the study as it was unable to provide input from an alcohol health worker (AHW). Recruitment was therefore restricted to three sites. Another clinic started to provide additional support for young people aged ≤ 18 years aimed at promoting sexual health. This intervention included discussion of alcohol use. We therefore changed our eligibility criteria to include only those aged ≥ 19 years.

We made one additional change to the study after commencement. The original sample size for the study was set at 320, which was judged to be large enough to detect clinically important differences in levels of alcohol consumption among those offered active and control treatment. In the first few months of the trial it became clear that the rate of recruitment was higher than we had originally anticipated. With the support of the funder and the independent Trial Steering Committee and following approval of the Research Ethics Committee we increased the sample size to 760 in order to have sufficient power to examine clinically important differences in our main secondary outcome: the proportion of participants who reported any unprotected sex at follow-up.

The public and patients were involved at several stages of the study (see Appendix 1 for further details).

Study setting and sample

Study participants were recruited from three sexual health clinics in central and west London. These clinics serve a diverse population of over 500,000 people with high levels of alcohol misuse and poor sexual health. 22,23

To participate in the study people had to be aged ≥ 19 years, be drinking excessively according to the Modified-Single Alcohol Screening Question (M-SASQ)24 and be willing to provide written informed consent to take part in the study. We excluded any person who was unable to communicate in English sufficiently well to complete baseline questionnaires, anyone who did not have an address or contact telephone number and anyone who believed they may not have been contactable in 6 months’ time.

Study interventions

The SHEAR had two treatment conditions: brief intervention for excessive use of alcohol and control treatment.

Treatment fidelity

In order to assess treatment fidelity, clinicians delivering brief advice and AHWs were asked to complete a treatment proforma for each person they saw. These proforma can be found in Appendices 2 and 3 of this report. The proforma completed by clinicians was based on one we used in a previous trial. 16 Front-line clinicians were asked to indicate whether or not they had delivered each of the four components of brief advice and AHWs were asked to complete a longer proforma which recorded the number and length of session(s), interventions delivered during the session(s) and further information of referrals that were subsequently made. A member of the research team was on hand to check completion of these proforma and to support and advise clinicians on delivering brief advice if required. Proforma were examined at the end of the study to identify the proportion of those in the active arm of the trial who received brief advice and brief intervention.

Outcome measures

Study procedures

Participant honoraria

Participants who completed the follow-up interview were offered a gift voucher for £15 in recognition of their help with the study and to compensate them for any inconvenience they experienced.

Sample size

In the absence of information on weekly alcohol consumption among people attending sexual health clinics we based our sample size calculation on data from a previous trial set in an emergency department. 16 We calculated that 97 evaluable participants would be needed per treatment arm to have 80% power to detect a difference in mean weekly alcohol consumption of 23.4 units with a standard deviation (SD) of 58.0 units (or 0.40 standardised difference), using a 5% level of statistical significance. However, a clustering effect may occur in the intervention arm due to different clinicians delivering the intervention. Power calculation formulae for a partially clustered design have been reported by Roberts and Roberts. 34 Based on an average cluster size of 7 and an intraclass correlation coefficient of 0.04 in the intervention arm, a total of 112 evaluable patients in each arm (16 clusters of 7 in the control group) would provide above 80% power to detect such a difference. This corresponds to an inflation factor for clustering (design effect) of 1.15. Expecting a 30% drop-out rate at 6 months, we therefore aimed to recruit 320 participants.

During the first few months of the trial it became clear that the rate of recruitment was higher than we anticipated; the sample size was therefore modified to provide additional power to test both the primary and main secondary hypotheses (a reduction in unprotected sexual intercourse).

The final sample size was based on a practical size of 380 per arm (760 in total). If 65% of participants had unprotected sex in the control group, compared with 50% in the intervention arm, the power to detect such an effect would be above 90%, assuming 25% drop out, and a clustering design effect of 1.15. The power would remain above 80% if the absolute difference was above 13%.

Statistical analysis

A detailed statistical analysis plan was developed and published online before analysis. 35 We used the statistical package Stata (StataCorp LP, College Station, TX, USA; version 12) for all of the descriptive analysis, graphs and regression models. All analyses were carried out according to randomisation arm (intention to treat), and two-sided p-values were considered significant when < 0.05. Descriptive analyses, including tables and graphs of baseline demographic and clinical variables, were conducted.

The primary outcome was compared between arms using random-effects linear regression adjusted for age (years), sex, clinic and M-SASQ measured at baseline. A random effect was included in the intervention arm to take into account any possible clustering by the clinician delivering the intervention, and residuals were allowed to differ by arm. This corresponds to the analysis suggested for partially nested trial design by Walwyn and Roberts. 36 Sensitivity analyses were then performed to confirm the validity of the result. Different hierarchical models were fitted and standard errors were calculated using approaches more robust to non-normally distributed residuals, such as robust standard errors or non-parametric bootstrapping. Ten thousand bootstrap resamples were obtained to achieve stable estimates. Results of direct mean comparison (t-test) and of adjustment for imbalanced baseline characteristics were also explored.

The main secondary outcome was analysed using random-effects logistic regression and adjusting for unprotected sex at baseline. As for the primary outcome, various sensitivity analyses were also performed. Other secondary outcomes were compared using appropriate regressions or tests and adjusted for age (years), sex, clinic and the corresponding outcome variable at baseline. As the addition of a clinician random effect was found to have little effect on results, it was ignored for the comparison of secondary outcomes.

Baseline data were missing for one participant, and mean imputation was used in this case for adjusted analyses. 37 Baseline characteristics of participants who dropped out from the trial were compared with the completers. Multiple imputation by chained equations was performed to impute the primary and main secondary outcomes at the follow-up visit. The imputation model included the important predictors of missingness and outcomes. Predictive mean matching was used to impute the alcohol consumption. Imputation was performed stratified by randomisation arm, and clustering by clinician was ignored in the imputation and analysis model. In order to reach negligible Monte Carlo error, 500 imputations were performed. Further sensitivity models allowing for missing not-at-random mechanism were also considered. 38 They were based on a pattern mixture approach, considering a large range of possible differences in outcomes between participants who completed the follow-up and those who did not. Mean difference and confidence intervals (CIs) were estimated using the ‘rctmiss’39 user-written command in Stata.

To assess for possible heterogeneity of the intervention effect, primary and main secondary outcomes are also reported by the following subgroups: gender, age (< 25 years, 25–35 years, > 35 years), number of sexual partners in the 6 months preceding baseline (1 vs. > 1), and sexual orientation (heterosexual vs. non-heterosexual). We then tested for the presence of an interaction term between the subgroups and treatment arm. Age (years) was additionally tested as a continuous variable and considered to have a linear effect in the regression. For participants in the intervention arm, the alcohol consumption was also described by categories of intervention received.

Economic analysis

Recruitment and randomisation

Study recruitment commenced in August 2010. Between August 2010 and May 2012, 1640 people were assessed for participation in the study. Recruitment stopped at this point as the revised target sample size had been exceeded and a decision was made to stop recruitment in a trial management meeting. Of the 1640 people assessed, 802 (49%) were eligible and willing to provide consent and were randomised. The reasons for non-participation were not willing to provide consent (n = 447, 53%), not drinking alcohol excessively (n = 369, 44%) and insufficient spoken English to complete the baseline assessment (n = 22, 3%) (Figure 1). Of the 802 people who took part in the study, 400 were allocated to the control group and 402 were allocated to brief intervention.

FIGURE 1.

Study flow chart.

Characteristics of the study sample

Sociodemographic and clinical characteristics of study participants at baseline are presented in Table 2. Participants were recruited from three hospital sites. Just under two-thirds of the participants were recruited from the West London Centre for Sexual Health based at Charing Cross Hospital, London, UK (hospital site 1; n = 495, 61.7%); one-quarter were recruited from the John Hunter Clinic for Sexual Health based at Chelsea and Westminster Hospital, London, UK (hospital site 2; n = 206, 25.7%); and the others were recruited from the Jefferiss wing based at St Mary’s Hospital, London, UK (hospital site 3; n = 101, 12.6%). Participants ranged in age from 19 to 55 years (median age 27 years) and just over half (54%) were female. Most participants presented to the service either because they were experiencing genitourinary symptoms or for a health check.

The results of the baseline assessment are presented in Tables 2 and 3 and show that, while the groups were generally well balanced, in the intervention group there was a lower proportion of heterosexual participants and a lower proportion who reported having had unprotected sex in the previous 6 months.

Flow of participants through the trial

The Consolidated Standards of Reporting Trials (CONSORT) diagram (see Figure 1) summarises the flow of participants through the trial. A total of 592 participants (73.8%) were followed up at 6 months. Of the 210 (26.2%) participants who were not followed up at 6 months, 61 (29%) formally withdrew from the study and the other 149 (71%) either could not be traced or did not take up repeated offers to be assessed.

Participants who did not complete the follow-up (n = 210, 26.2%) were on average younger (26.8 years old vs. 28.1 years old, p = 0.009) and with higher-risk sexual behaviour (e.g. 45.2% did not use a condom the first time they had sex with their last partner vs. 34.9%, p = 0.008) than those who completed the study. The attrition rate was not significantly different between arms (24.7% in the control group vs. 27.6% in the intervention group, p = 0.36). There were no significant differences in predictors of drop out between arms.

Masking of researchers conducting follow-up interviews

Researchers reported nine occasions when they became aware of a participants’ allocation status. All the participants were from the brief intervention arm of the trial. This occurred on each occasion because the participant told the researcher which arm of the trial they had been allocated to.

Uptake of allocated treatments

Four hundred and two participants were allocated to the brief intervention treatment, of whom 397 (99%) received the treatment. The brief advice was delivered by a total of 79 clinicians, each seeing a median of three trial participants [interquartile range (IQR) 1–6]. Three hundred and sixteen (79.9%) participants received brief advice only from the clinician and 81 participants (20.1%) received brief advice and an appointment with an AHW. Of those who had contact with the AHW, 33 (40.7%) met with the AHW for their appointment and the remaining 48 (59.3%) received advice and support over the telephone. Table 4 details the alcohol consumption at follow-up by intervention for participants in the intervention arm.

Treatment fidelity

Data from treatment proforma showed that, of the 402 randomised to brief intervention, 397 (99%) received brief feedback that alcohol use at that level has the potential to harm health; 370 (92%) were asked whether or not there was a link between alcohol use and attendance at the clinic; 397 (99%) were given a leaflet on alcohol and health, of whom 372 (92.5%) took the leaflet; and 397 (99%) were offered an appointment with an AHW.

Main and secondary outcomes

Primary and secondary outcomes at the 6-month follow-up are described in Table 5. In the intervention arm, weekly alcohol consumption was 2.33 units lower and fewer participants than in the control arm reported having unprotected sex.

Table 6 shows the effect of allocation to the intervention arm compared with the control treatment. At 6 months, participants allocated to brief intervention had a reduction in mean weekly alcohol consumption (adjusted mean difference –2.33 units/week; 95% CI –4.69 to 0.03 units/week; p = 0.053). This difference corresponds to a –0.14 standardised effect size (SD = 16.1). There was no evidence of a difference in the proportions who had had unprotected sex in the past 3 months [adjusted odds ratio (OR) 0.89, 95% CI 0.63 to 1.25; p = 0.496]. For other secondary outcomes, only the average number of units drunk per drinking day showed a statistically significant result (difference –1.13 units/drinking day; 95% CI –1.96 to –0.29 units/drinking day; p = 0.009), suggesting that during drinking days the intervention group drank fewer units on average than the control group.

Sensitivity analyses

The results of the different sensitivity analyses models are reported in Appendix 5. For the primary outcome, results were all consistent with there being a small difference in weekly alcohol consumption between the treatment arms, which was close to statistical significance. The bootstrap bias-corrected and accelerated CIs for the mean difference was –4.55 to 0.31. None of the calculated CIs included a difference between the treatment arms of ≥ 5 units. For the main secondary outcome, results were also consistent between sensitivity analyses, giving an OR of around 0.90, except when the difference in unprotected sex at baseline was not accounted for or ignored (OR = 0.78). None of the results were statistically significant at the 5% level.

Missing data

Baseline data were missing for only one participant and were imputed using mean imputation. Meanwhile, data for 210 patients were missing at the final follow-up owing to withdrawal and loss to follow-up: 99 in the control group and 111 in the intervention group (see Figure 1). After multiple imputation of these missing outcomes, the adjusted mean difference in the primary outcome was –2.43 (95% CI –4.73 to –0.13; p = 0.038) and the OR for the main secondary outcome was 0.89 (95% CI 0.63 to 1.25; p = 0.494) (see Appendix 5).

The results of a sensitivity analyses based on the assumption that outcome data were missing non at random are reported for the primary outcome and main secondary outcome in Appendix 6. The primary outcome result could differ if there is an important difference in the response pattern between the arms; however, in the more plausible scenarios the mean difference remained small (between –4 and 0 units per week). In the most extreme scenario missing control group participants were assumed to drink, on average, 15 units per week more than control group participants who completed follow-up, whereas intervention group non-completers were assumed to drink on average 5 units per week less than their completer equivalents. Under this scenario, the difference in mean alcohol consumption between the groups could be as high as –7.17 units per week. For the main secondary outcomes, all scenarios gave a non-significant difference between arms, with an OR likely to remain between 0.8 and 1.0.

Subgroup analysis

Differences in primary and main secondary outcomes by subgroups are reported in Figure 2 and Table 7. There was a possible trend for the intervention to be more effective in reducing unprotected sex with increased age, although the result was not statistically significant and has to be interpreted in consideration of the multiple comparisons and low power of the interaction test.

FIGURE 2.

Forest plot of difference in primary and main secondary outcome by subgroups. (a) Difference in weekly alcohol consumption; and (b) OR of unprotected sexual relations.

Economic evaluation

Cost

Mean cost of services per participant over 6-month follow-up is detailed in Table 9. There was no difference in service cost between those randomised to the control condition (£310.87) and those randomised to brief intervention (£319.28, p = 0.879). The cost of the brief intervention was on average £12.57 per participant, which represented around 4% of total service costs. The average cost per participant for outpatient STI appointments was £23.97 in the control group and £25.55 in the brief intervention group. Imputation of missing data did not alter the direction or difference in total costs [control (n = 400) £311.13; brief intervention (n = 402) £319.64, p = 0.835].

Economic outcomes

Quality-adjusted life-years are detailed in Table 10. Mean QALYs were similar between groups at 6-month follow-up and there were no statistically significant differences in EQ-5D scores or QALYs. Units of alcohol per week for those with complete economic data were 20 in the control group and 18 in the brief intervention group.

Cost-effectiveness

There were no significant between-group differences in costs or outcomes. QALYs over follow-up were 0.007 lower in the brief intervention group, and costs were £8.41 higher, which results in a negative incremental cost-effectiveness ratio (ICER) of –£1200.00 per QALY, suggesting that the control dominates the brief intervention. For the alcohol consumption outcome, 2 fewer units per week were consumed on average in the brief intervention group and costs were £8.41 higher, resulting in an ICER of £4.20 per unit reduction in weekly alcohol consumption. Given the lack of statistical significance in these ICERs, attention needs to be given to uncertainty represented in the scatterplots and CEACs presented below.

The bootstrapped replications for costs and QALYs are shown on a cost-effectiveness plane in Figure 3. Most of the dots lie to the left of the x-axis (brief intervention associated with worse outcomes than control) and above the y-axis (brief intervention associated with higher costs than control) suggesting that the brief intervention is not cost-effective. The CEAC (Figure 4) confirms this finding, for willingness-to-pay values for a QALY up to £30,000 there is no more than a 42% probability that brief intervention is more cost-effective than the control treatment.

FIGURE 3.

Cost-effectiveness plane for the comparison of the brief intervention and usual care, based on 10,000 bootstrapped cost–effect pairs, using QALYs.

FIGURE 4.

Cost-effectiveness acceptability curve showing probability that brief intervention is cost-effective compared with usual care for different values of willingness to pay per QALY.

The bootstrapped replications for costs and alcohol consumption are shown on a cost-effectiveness plane in Figure 5. Most of the dots lie to the left of the x-axis (brief intervention associated with better outcomes) and above the y-axis (brief intervention costs higher), suggesting that the brief intervention could be cost-effective, depending on society’s willingness to pay for a unit reduction in weekly alcohol consumption. The CEAC (Figure 6) summarises information on willingness to pay and cost-effectiveness. If society places a value of zero on its willingness to pay for a unit reduction in alcohol consumption, then the probability of brief intervention being more cost-effective than the control treatment is 44%. However, if society is willing to pay up to £5 per unit reduction in alcohol consumption then the probability of cost-effectiveness increases to over 50%.

FIGURE 5.

Cost-effectiveness plane for the comparison of the brief intervention and usual care, based on 10,000 bootstrapped cost–effect pairs using weekly alcohol consumption.

FIGURE 6.

Cost-effectiveness acceptability curve showing probability that brief intervention is cost-effective compared with usual care for different values of willingness to pay per unit reduction in weekly alcohol consumption.

Study findings

Data from this randomised trial of brief intervention for excessive alcohol use among people attending sexual health clinics suggest that there is little, if any, difference in alcohol consumption between those who are and are not offered this intervention. Follow-up data collected from 592 (74%) of the 802 participants at 6 months showed that those who were randomised to brief intervention were drinking a mean of 2.3 units (18.4 g) of alcohol less per week than those randomised to the control group. Interpreting results of trials with borderline significance is not straightforward. In keeping with the recommendations of Hackshaw and Kirkwood,50 we base this conclusion on the clinical significance of the changes we found rather than on the probability of the difference being the result of chance. Although a statistically significant difference in the number of units of alcohol per drinking day was observed, the scale of the difference (1.1 units/8.8 g) is unlikely to be clinically important. Significant differences in sexual health outcomes were not found between the groups, though we cannot rule out the possibility that brief intervention could be associated with small, but clinically important, changes in sexual health outcomes. At less than £13.00 per participant, brief intervention was inexpensive. When other costs and outcomes were taken into account we found little evidence that the intervention would provide a cost-effective use of resources. The results of the cost-effectiveness analysis suggest that if a service were to be willing to pay £5.00 for a weekly unit reduction in alcohol consumption, the brief intervention would have a > 50% chance of being cost-effective. However, the relevance of this interpretation is difficult since we know that a weekly reduction in alcohol consumption is not a clinically meaningful change.

Strengths and weaknesses of the study

The rate of recruitment to the study was higher than we initially anticipated. With the approval of the independent Trial Steering Group, Data Monitoring Committee and Research Ethics Committee and the support of the study funder we increased the planned sample size to increase the statistical power that we had to examine the impact of the intervention on our secondary outcomes. The sample of over 800 participants was large enough to detect clinically important changes in alcohol consumption and moderate to large changes in sexual behaviour. The rate of follow-up we achieved was also higher than we had planned, with 74% of all participants followed up at 6 months. Two other notable strengths of the study relate to the recruitment and assessment process we used and the type of intervention received by those in the active arm of the trial.

Recruitment to the study involved asking potential participants if they would be willing to take part in a study of ‘sexual health and lifestyle’. Written and verbal information given to participants made no explicit reference to alcohol use. When assessing whether or not potential participants were eligible to take part, we used a single question on alcohol use which was embedded in a series of other questions about smoking, exercise and diet. By using this approach we were able to reduce exposure to prompts about alcohol use which could have encouraged those in the control arm of the trial to reflect on their use of alcohol and consider reducing this. In doing so, we believe that we have replicated normal clinical practice in sexual health clinics where information about alcohol is not normally collected. Previous trials of brief intervention for alcohol misuse have been criticised for underestimating the effects of screening and intervention by exposing control participants to more detailed questions about alcohol, which may in themselves lead to reductions in alcohol consumption. 51

We based our intervention on a form of brief advice which is acceptable to staff working in busy clinical settings and can be delivered in under a minute. 52 Evidence for the acceptability of the approach was found by data from the active arm of the trial showing that almost 99% of people received brief advice. This approach does not require clinicians to deliver anything other than very simple advice to accompany a leaflet on alcohol and health and the offer of more intensive advice and support for those who want it. By testing an approach to intervention which was delivered by front-line clinicians rather than specially trained staff, we believe that we took a pragmatic approach to testing an approach to helping people who consume excessive alcohol which had the potential to be delivered widely as part of routine clinical practice.

The study has a number of limitations which should be considered when interpreting the findings. Although we recruited more participants than we planned, these were all from three sexual health clinics in inner and central London. Although this area covers over 500,000 residents from a range of different socioeconomic backgrounds, we do not know if our results would have been the same had participants been recruited from other parts of the country.

In our effort to maximise recruitment in this busy clinical setting and minimise exposure to prompts about alcohol use for control participants we used a very short baseline assessment which did not involve collecting detailed information about alcohol use or service utilisation. This meant that we had limited data to compare the characteristics of those in the two arms of the trial or information that could be used to impute follow-up data on those from whom this was not obtained.

Although we used validated outcome measures that have been widely used in previous trials, these were based on the self-reporting by study participants. We do not know the extent to which they provide an accurate measure of actual behaviour. In addition, the economic evaluation used the EQ-5D to measure quality of life, which has been shown to be insensitive to changes in levels of alcohol consumption amongst hazardous drinkers.

At 74%, the rate of follow-up we achieved is similar to that of other trials of brief intervention for alcohol misuse in secondary care settings. 16,21 This remains an important level of attrition, and the intervention effect observed in the completers could be a biased estimate of the effect in all participants, especially if the intervention had a different effect in the non-responders, or if the intervention affected the chance of response. However, the response rate was not highly different between the arms, and we perform different sensitivity analyses to see how missing data could have affected the results. Although the intervention effect estimate could be affected by the missing data, it appeared unlikely that the overall conclusions of the trial would change.

Only a minority of those in the active arm of the trial received brief intervention from an appointment with the AHW. This level of uptake of brief intervention is far higher than in a pilot study we conducted. 9 We believe that one of the reasons for this was that AHWs offered telephone-based intervention that did not require participants to come back to the clinic.

Comparison with results of other studies

Very little research has been conducted to examine the impact of intervention for excessive alcohol use among people attending sexual health services. Lane and colleagues compared the effects of brief intervention for risky drinking delivered by a trained nurse in a sexual health clinic in Sydney, Australia, among 184 people. 21 They found a small, non-statistically significant difference in the proportion of people drinking harmfully among those who did and did not receive a brief intervention. Three months after randomisation, 46% of those in the active arm of the trial and 39% in the control arm were drinking excessively according to AUDIT-C (a three-item quantity frequency measure of alcohol consumption derived from the 10-item Alcohol Use identification test). These small differences in levels of alcohol consumption between treatment arms are of the same order of magnitude as the differences we found in this study. We are aware of two other trials of brief intervention for alcohol among people who attend sexual health clinics and are drinking above recommended limits, but neither has so far published their findings.

In contrast, a large number of studies have been conducted across a range of other health-care settings including primary care, emergency departments and specialist clinics. Findings from these trials have generally shown that brief intervention is associated with clinically important reductions in alcohol consumption over a 6- to 12-month period. In a systematic review of 22 clinical trials, Kaner and colleagues reported a standardised mean difference of 5 units of alcohol per week at 6 months among those who received active compared with control treatment. 53 Changes in alcohol consumption of this magnitude also seem to be associated with reductions in all-cause mortality.

There is no agreement about what constitutes a clinically significant reduction in alcohol consumption. However, other clinical trials have been powered to detect differences of between 3.5 and 10 units of alcohol per week. 16,54 Other trials have been powered to detect clinically important differences in the proportion of people drinking excessively; such trials have been powered to detect differences in proportions in the region of 13%12,55,56 rather than the difference of 5.8% that we found in this study. It is unclear why larger differences in alcohol consumption were not found between the active and control arms of the SHEAR trial. Possible reasons for this include the level of alcohol misuse among people attending sexual health clinics, the intervention that people received and readiness to change.

Level of alcohol misuse among study participants

Previous research has established high levels of alcohol consumption among people attending sexual health clinics. As many as 70% of attendees are drinking above recommended levels. 10 In our study, 68% of the attendees who completed the baseline questionnaire were drinking excessively according to the M-SASQ criteria. We did not collect detailed information about the level of alcohol consumed at baseline. However, at follow-up, information on alcohol consumption over the previous 12 weeks revealed that participants were drinking a median of 15 units of alcohol a week – well below recommended maximum levels of weekly alcohol consumption. With a median of 10 units per drinking day, most study participants were regularly exceeding recommended limits for drinks per day and over three-quarters were therefore classified as ‘drinking excessively’ according to the M-SASQ criteria. However, overall levels of alcohol consumption were far lower than that seen in other intervention studies conducted in primary and secondary care, where study participants were reported to be drinking three or four times as much as SHEAR participants. 16,53 There is some evidence that brief intervention is less effective among people have lower levels of alcohol consumption. 53 By recruiting participants whose level of alcohol consumption may not have been as high as that in emergency departments and other hospital settings the likelihood of demonstrating clinically significant reductions in alcohol consumption may have been reduced.

Treatment fidelity

The intervention that we used in the SHEAR trial was designed to meet national recommendations for brief alcohol intervention and was modelled on that used in a previous trial which demonstrated positive effects. However, it could only have been effective if it was delivered in the intended manner. Data collected from treatment proforma indicate that nearly all those allocated to the intervention received each of the four components of brief advice that they should have been offered.

It has been argued that, in order to be effective, those delivering brief interventions need to have a positive attitude to the information they provide. 57 A survey of all clinicians who delivered the brief intervention that we conducted parallel to the trial demonstrated that the majority believed that there was a link between alcohol use and sexual health, and that the intervention they were asked to deliver had the potential to help improve sexual health. Available data therefore suggest that the intervention was delivered in the manner intended and that the largely negative findings of the trial are not the result of the way the intervention was delivered.

Readiness to change

The opportunity to help a person reduce his or her use of alcohol when presenting to services with health problems that may be related to excessive alcohol use has been called a ‘teachable moment’. 58 Emergency departments may provide an effective point at which to intervene because the link between alcohol use and negative effects on health such as gastrointestinal problems, accidents, injuries and deliberate self-harm are closely related at the points at which the intervention is provided. In specialist settings, such as maxillofacial clinics, a patient may have a clear sense of a causal link between excessive alcohol consumption and physical trauma. 13 There is some evidence that people using sexual health clinics, while acknowledging a link between alcohol use and sexual behaviour, do not view this as one in which alcohol use leads to STIs or other negative health consequences. In semistructured interviews with 100 women attending sexual health and family planning clinics, Taylor and colleagues reported that participants rarely believed that alcohol consumption had led them to engage in sexual behaviour which they would not have engaged in had they not been drinking. 59 Instead participants said that sexual encounters tended to take place in environments where alcohol and/or drug use were likely to occur or they used alcohol instrumentally to engage in desired sexual behaviours.

We are in the process of analysing qualitative data from study participants which may help us develop a better understanding of why clinically important changes in alcohol consumption were not found in the study. Data analysis is ongoing and a report will be completed in 2014, but our impression thus far is that people attending sexual health clinics and drinking above recommended daily units of alcohol do not view the amount they consume as excessive. Instead it is seen as a normal part of their social life and a means of having fun. These observations are supported by a secondary analysis of data from brief advice proformas showing that 19% think that their attendance in the clinic could be related to their use of alcohol (compared with over 69% of those in our previous study in an emergency department). Although people attending sexual health clinics may want to achieve better sexual health, attempts to reduce alcohol consumption are generally not seen by them as a necessary means of trying to achieve this aim.

Implications for services and future research

The results of this study do not support the routine use of screening and intervention for excessive alcohol use among people attending sexual health clinics. Although assessment of alcohol use as part of wider efforts to help some people with poor sexual health take steps aimed at reducing risky sexual behaviour makes sense, universal use of screening and delivery of brief interventions does not appear to provide a clinically effective or cost-effective use of available resources.

It is, however, possible that there are subgroups of people for whom brief alcohol intervention would be helpful, for instance individuals with high levels of acquisition of new STIs in the context of high levels of alcohol misuse and those seeking human immunodeficiency virus (HIV) post-exposure prophylaxis or emergency contraception. Further research examining the impact of brief alcohol intervention among such groups is warranted. We recommend that such studies set a higher threshold of excessive alcohol consumption to determine entry into the study than the one we used (such as drinking above recommended limits on a weekly, rather than a monthly, basis).

We excluded people aged < 19 years from the trial. Levels of alcohol misuse may be higher among teenagers attending sexual health clinics than among adults and future research should develop and test the impact of age-appropriate methods to help young people reflect on, and reduce, their use of alcohol.

Data suggesting that population-based interventions that lead to lower levels of alcohol consumption also have an impact on levels of new STIs are also important. There is currently a debate about public health measures aimed at reducing alcohol consumption, such as setting a minimum price per unit alcohol. Such changes may have an impact on rates of STIs and, if introduced, future studies should examine the impact of these changes on sexual health outcomes.

Contributions of authors

Mike J Crawford (Professor, Health Services Research) was the chief investigator of the SHEAR trial.

Mike J Crawford together with Rahil Sanatinia (Research Assistant, Mental Health Research) and Robin Touquet (Emeritus Professor, Interventions for Alcohol Misuse) designed the study with input from Barbara Barrett (Lecturer, Health Economics), Baptiste Leurent (Research Associate, Medical Statistics), Sarah Byford (Professor, Health Economics), John Green (Head of Psychology CNWL, Sexual Health), Michael Sweeting (Research Associate, Medical Statistics), Anne Lingford-Hughes (Professor, Addiction), Peter Tyrer (Professor, Health Services Research) and Helen Ward (Professor, Public Health).

Rachael Jones (Consultant Physician, Sexual Health) helped liaise with clinical services and oversee recruitment.

Baptiste Leurent, Michael Sweeting and Mike J Crawford designed the statistical analysis plan.

Outcome data were analysed by Baptiste Leurent with guidance from Michael Sweeting.

Sarah Byford designed the economic component of the trial and supervised the conduct of the economic evaluation.

Barbara Barrett carried out the cost-effectiveness analysis. Rahil Sanatinia recruited participants from all three sites with assistance from Shreena Ghelani and Lorraine O’Connell.

Madeleine Dean (Research Assistant, Psychology) completed follow-up interviews with assistance from Bianca Hinds-Walters and Raphael Underwood.

All study authors contributed to the preparation of this report.

Disclaimers

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. 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, NETSCC, the HTA programme or the Department of Health.

Publication

Sanatinia R, Barrett B, Byford S, Dean M, Green J, Jones R, et al. Brief intervention for alcohol misuse in people attending sexual health clinics: study protocol for a randomised controlled trial. Trials 2012;13:149.

Missing not-at-random results

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