Screening in brief intervention trials targeting excessive drinkers in general practice: systematic review and meta-analysis

Identifying studies

AB and TT searched the electronic databases, checked reference lists of earlier reviews and retrieved papers, hand searched, and consulted European experts. They then defined a final electronic search strategy (box 1) and criteria for inclusion (box 2). Medline, Embase, PsycInfo, Cochrane, and ETOH databases were searched without time limits for reports in English language on controlled trials.

Assessing validity

Internal validity—We assessed four types of bias in each study included in the meta-analysis (selection bias, performance bias, attrition bias, detection bias; see table 2).19 20 The validity assessment was used only for the discussion of differences between studies and possible bias of findings.19

External validity—We used an adaptation of Feinstein's model (1) to assess losses from screening to follow up.20 This categorises the excessive drinkers available for screening (users of the healthcare system, those not refusing screening, not physically or psychologically impaired, not illiterates, etc) into five groups.

Fig 1

From intended population to admitted group

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Assessing outcomes

Absolute risk reduction (in this case an increase in benefit) is the difference between proportions of individuals reporting to be drinking below weekly limits at follow up when groups were comparable at baseline. To compute the event rates we used an intention to treat approach with the total number of randomly assigned patients as the denominator.21 Twelve months' follow up was the typical period, and we used it for comparison purpose in the meta-analysis. CIA software (Wilson method) was used for computing confidence intervals.22

Number needed to treat equals 1 divided by the absolute risk reduction. We gave confidence intervals as suggested by Rembold,17 with negative values indicating harm and positive values indicating benefit. For example, an NNT of +20 means that an extra patient benefits for every 20 patients treated with the “new intervention.”22

Screening effect—To describe the effect of screening we estimated the number of positive events per 1000 patients screened. This figure shows the proportion of patients who will benefit from the programme. The screening effect is estimated as the product of the prevalence of a treatable condition and the absolute risk reduction from treatment.17 In our case, the prevalence is the number admitted for brief intervention divided by the number screened. These prevalences are kept fixed and not considered to deviate due to chance in our estimations since they are primarily determined by the screening and assessment procedure of the single study rather than by any stochastic variation.

Summarising effects across studies

We used the fixed effect Mantel-Haenszel pooling method and the matching heterogeneity statistic for combining results from the different studies.23 To test the sensitivity of the pooling method we replicated the estimations using a random effects model. The pooled NNT value and corresponding 95% confidence interval were obtained by inverting the pooled risk difference value and its interval. The pooled screening effect value and its 95% confidence interval were established by multiplying the average weighted prevalence with the pooled absolute risk reduction and its confidence intervals.

Inclusion and description of studies

Of 309 hits on Medline, 19 papers could be included, according for attrition mapping (table 1). PsycInfo (Silverplatter) contributed one additional paper.24 One of the 20 papers reported long term follow up of a trial already included, and it was not included for further assessment.25 We mapped the 19 studies according to the different types of attrition from screening to follow up and estimated the numbers for each type of attrition.

In general, a high percentage of patients who screened positive were excluded by protocol, refused further participation, or were not included for unspecified reasons during a secondary assessment carried out by a researcher and taking place before the randomisation. Typically, a few patients with severe alcohol problems or false positive screening results were excluded by protocol; the reasons commonly given were low compliance, comorbidity, or were not specified.

Inclusion in meta-analysis

Two of the 19 studies did not report the number screened to obtain subjects for randomisation.18 26 Another nine (of which seven did not find any statistically significant differences on drinking outcome measures) failed to fulfil the fifth criteria by not reporting an event outcome measure and were not included for meta-analysis.27^–35 The meta-analysis included eight of the largest studies (2); one of these was a subgroup analysis that did not contribute to the pooled effect values.36

For screening, all eight studies used general health or lifestyle questionnaires that included questions on alcohol consumption. Questionnaires were provided to patients when they came to visit their doctor. Four studies also invited patients by mailing out questionnaires,24 37^–39 and one study telephoned patients.37

The interventions that were provided ranged from a 10 minute consultation24 39 to up to five consultations lasting 5-20 minutes.40 The intervention protocols all included feedback on present drinking, education on risk and strategies for changing drinking, and the practitioner's advice to cut down on drinking.

Methodological quality

3 shows the four key components of study validity.19 23 One study randomised four participating practices rather than patients37 and another one used weekly shifts between intervention and control periods.40 All studies found sufficient blinding impossible.

In general, follow up rates were high and the US studies all had follow up of 85% or more.36 37 41 42 The TrEAT group studies36 41 42 did not state their sample size considerations; their goal for consumption after treatment was more liberal than the criteria for excess drinking at screening, and follow up rates differed considerably between allocation groups in two of these studies (90% v 97%; P = 0.000241 and 94% v 100%; P = 0.03936; table 3). The large UK study by Wallace et al had a lower follow up rate for the male intervention group (83% v 89%; P < 0.05).38

Heterogeneity

The studies varied slightly regarding inclusion criteria and baseline prevalence. However, the outcome results were not significantly different (test for heterogeneity χ² = 8.9, df = 6, P = 0.18). As this P value is clearly above 0.10 we accepted the fixed effect approach as sufficient to produce an average measure of treatment effect and reliable confidence intervals.19 43 We used a random effects model (RevMan software44) to investigate the robustness of the fixed effect approach.

Intervention effect and assessment efforts

The pooled absolute risk reduction was 10.5% (95% confidence interval 7.1% to 13.9%) (4). A random effects model yielded a similar result: 10% (6% to 14%).

The pooled number needed to treat (NNT) was 10 (7 to 14). NNTs of single studies ranged from 5 to 61 and all results favoured intervention to some degree (4). Two studies had notably higher NNTs,24 37 and the 95% confidence intervals of five studies include the possibility of harm.24 36 37 41 42

All NNT values have to be interpreted in the light of the screening and assessment activity that took place to establish the trial sample as well as the character of the outcome in question. Nine per cent of patients (12 327/134 693; range in individual studies, 3.3% to 18%) screened positive; further assessment identified 2.5% (3317/143 693; range 0.9% to 5.4%) who were given brief interventions.

American and British studies defined sensible drinking differently. The US studies included people who drank less than in the UK studies (table 2). The TrEAT group studies had intervention goals for sensible drinking that were more liberal than the ones they used in their inclusion criteria,36 41 42 whereas the studies from Britain and Australia all had goals for sensible drinking that were more strict or equal to their inclusion criteria limits.

Giving up binge drinking is another possible outcome of intervention. Table 5 shows the screening effect values for this event in the six studies that reported this outcome. However, a strong interdependence between reduced drinking overall and lack of binge drinking is likely, so that giving up excessive weekly consumption also “cures” binge drinking. Only one of the eight studies reported a combined outcome of “safe weekly drinking and non-binge drinking.”37 In that study giving up excessive drinking reduced binge drinking while the number of “pure” binge drinkers remained unchanged in both groups.

Screening effectiveness and programme outcome

The pooled screening effect was 2.6 (1.7 to 3.4) patients per 1000 screened for achieving sensible drinking (based on the weighted average of admission to brief intervention of 2.46%). In single studies, values for screening effects varied from 0.1 to 6.2 patients per 1000 screened (4).

The average pooled screening effect was sensitive to differences in the prevalence of participants admitted to receive brief intervention. This prevalence varied between 0.9% and 5.4% in the studies we included. With an average risk reduction of 10.5% (7.1% to 13.9%) the corresponding screening effect would be 0.9 (0.6 to 1.3) patients per 1000 screened for the prevalence of 0.9% and 5.7 (3.8 to 7.5) patients per 1000 screened for the prevalence of 5.4%.

2 shows the results of the single studies and the pooled estimate. All results favour screening and intervention to some degree, the results seem to be quite homogeneous, and the pooled estimate is clearly significant.

Fig 2

Effect of screening for excessive drinking: number of patients with a positive outcome (reduction in drinking to below maximum recommended limits) per 1000 screened

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Discussion

If a practitioner screens 1000 patients, carries out further assessment in 90 patients (9%) who screen positive, and gives feedback, information, and advice to 25 (2.5%) who qualify for brief intervention, two or three patients can be expected to have reduced their alcohol consumption to below recommended maximum levels after 12 months.

Methodological considerations

We discovered several sources of bias, all tending towards overestimation of effect: impossibility of blinding patients and practitioners, combined with self reported outcome measures45; three papers did not report their sample size calculations and redefined excessive drinking at follow up36 41 42; one paper, which reporting better results than the others, had a shorter follow up37; and the two largest studies may have been affected by attrition bias.38 41 Self selection (through mailed and telephone invitations) in some studies24 37^–39 may have compromised their external validity.

We assumed that the reasons for exclusion and dropout after a positive result on screening in the studies were similar to the reasons for the practitioner or the patient choosing to undergo no further assessment or intervention—these being previous attempts to give advice, non-compliance with advice, refusal to attend for intervention, or a false positive screening result. In real life, screening could have a side benefit, identifying some cases of alcohol dependency not known to the doctor; some of these patients might be willing to be referred for treatment. That screening itself is beneficial is an assumption that remains untried, and counterproductive effects from alienation and badly timed screening have to be considered.

Pooled numbers needed to treat derived from meta-analyses can be misleading.46 For NNTs to be comparable, they must define patients' condition and its severity and the intervention, its outcome, and the setting, which they did in the present analysis. Nevertheless cultural, age, and sex differences should be taken into consideration, and single studies might contribute valuable information that should not be eclipsed by pooled estimates. Although the study by Anderson and the TrEAT trial both attempted to exclude people who were highly dependent on alcohol, the nature of the “events” might differ between men who drink heavily (included if > 29 drinks; mean consumption 44 drinks, goal 18; screening effect 3.7 per 1000)39 and less heavy drinkers (included if > 14 drinks; mean 22, goal 20; screening effect 2.6 per 1000).41 Positive net benefit is still possible when the screening effect is 2.6 per 1000 screened. The TrEAT study group has published an economic analysis showing a benefit-cost ratio of 5.6 (0.4 to 11.0).47 Aside from methodological problems and the crudeness of such a measure, one crucial problem remains. Screening for excessive drinking is in keen competition with other proposals for screening and prevention. A recent paper points out that a doctor in primary care needs 7.4 hours per working day to provide the preventive services recommended by US Preventive Services Task Force.48 Family doctors would have to give up other activities to free resources for a programme that would result in safer drinking habits for only a handful of their patients.

Drinking and general practice

The literature on brief intervention documents that a patient who is drinking excessively may reduce their alcohol consumption once a practitioner speaks to them. But if change occurs in only two or three of 90 patients who screened positive and were assessed further, the practitioner who screened 1000 patients to find those 90 could perceive this as a 97% disappointment rate.

Conversations about drinking may take place in many ways in general practice. Sensitively raising the subject, or facilitating patients' initiatives, may be a key characteristic of good clinical practice. Future research might focus on how a well established helping relationship can cover drinking related problems and risks in a way that benefits the patient and appeals to the practitioner.

The Medical Research Council suggests a stepwise framework for developing and evaluating randomised controlled trials for complex interventions to improve health.49 This approach includes modelling and exploratory research phases defining constant and variable elements of interventions, as well as evaluating the effectiveness of programmes in actual practice.

In the meantime, we propose a focus on the fact that information and advice is sometimes helpful, especially when rapport has been established and the agenda agreed on. Assessment of drinking, not only in groups with obvious alcohol related problems but also in groups of patients with symptoms correlated with high consumption (hypertension, dyspepsia, depression, injuries, social problems, etc), lies within the doctor's role. To help patients change their lifestyle, practitioners need and want supplementary training. These processes of improving good clinical practice could also be considered complex interventions, and trials could be developed accordingly.

Conclusions

Although even brief advice can make a difference, this review calls into question the model of universal screening in general practice as a case finding approach. Alcohol screening, assessment, and intervention are laborious and time consuming activities that only two or three people out of 1000 screened will benefit from. A practitioner who experiences such a low ratio of success to workload is bound to be disappointed and reluctant to engage any further even though the screening approach is consistent and utilitarian by nature and may seem beneficial from a population perspective.

Future research should focus on other ways than systematic screening of addressing excessive drinking among patients in general practice. More attention should be paid to the preconditions of and skills for successful interviewing, exchange of information, advice giving, and counselling.