We conducted literature searches up to September 2013 in the following bibliographic databases: MEDLINE, PsycINFO, Science Citation Index Expanded, Social Sciences Citation Index, Arts and Humanities Citation Index, CINAHL, PUBMED and EMBASE, using key words and text words. Words indicating online interventions (Internet, Web, online, computer, mobile) were combined with terms indicative of type of treatment (self-help, brief intervention, treatment, unguided, guided, supported, low-intensity) and problematic alcohol use (alcohol abuse, alcohol misuse, problem drinking, hazardous, harmful, dependence, abstinence). We also re-examined exclusion lists of papers retrieved for our previous meta-analysis [26] to see if any would meet the inclusion criteria for the current study. No language restrictions were applied.

Our initial selection was based on titles and abstracts. If these yielded insufficient information to assess the eligibility criteria, full-text articles were retrieved and assessed in terms of our inclusion criteria. All papers included or excluded at all stages were assessed by two independent raters (authors HR and HH) (see figure 1). The same raters assessed the effect sizes and moderator variables in the included studies. Any disagreement was resolved by discussion. A protocol does not exist for this meta-analysis; steps undertaken are described in this method section.

Randomised controlled trials were included that (1) compared a web-based intervention with a control group (in an assessment-only, waitlisted or alcohol information brochure control condition); (2) included a low-intensity self-help intervention that the participant could perform on a computer or mobile phone, with or without guidance from a professional; (3) assessed alcohol drinking behaviour in terms of quantity consumed as a primary outcome measure; (4) studied adults aged 18 or older; (5) included alcohol drinkers who exceeded local guidelines for low-risk drinking (if lower-risk participants were also included, we retained only the results of those with alcohol misuse).

We assessed the validity of the included studies on the basis of four criteria from the risk-of-bias assessment tool developed by the Cochrane Collaboration [39]. It verifies study attributes in randomised controlled trials that are potential sources of bias, including (1) adequacy of allocation sequence generation, (2) concealment of the allocation to the different conditions, (3) blinding of assessors and outcomes and (4) handling of incomplete outcome data using intention-to-treat analyses (this was rated as positive if intention-to-treat analyses were performed, thus retaining all randomised participants in the analyses; see table 1). Authors HH and MB assessed risk of bias as Yes, No or Unclear using the Cochrane Collaboration tool (see 2.3).

Characteristics of the analysed studies are described in table 1. We coded (1) year of study and country of origin; (2) participant characteristics: alcohol consumption level at baseline, recruitment setting, target group; (3) intervention characteristics: therapeutic principles, mode and setting of delivery, guided or unguided self-help format, number of sessions; and (4) other study characteristics: type of control condition, number of participants in each comparative condition, primary outcome measure (how consumed quantities of alcohol were assessed), intention-to-treat (ITT) versus completers-only (CO) analyses, post-treatment assessments in months, dropout rate and risk of bias. The brief self-help alcohol interventions we identified were based on one or more of the following principles: behavioural self-control [40], motivational interviewing [41], transtheoretical model of change [42], cognitive-behavioural therapy (CBT, [43]), and personalised normative feedback (PNF [44]).

We first calculated a mean alcohol consumption effect size for each comparison between an alcohol intervention and a control group. Effect sizes were calculated by subtracting the average post-test score of the alcohol self-help group from the average score of the comparison group and dividing the result by the pooled standard deviations of the two groups. This effect size is known as Cohen’s d. As the effect size d is subject to small-sample bias, it can be adjusted by using a scaling factor, which is multiplied by d to arrive at Hedges’s bias-corrected effect size g, so that g = d (1−[3/4(n₁+n₀]−9). An effect size of 0.50 indicates that the mean of the experimental group is half a standard deviation larger than the mean of the control group. Effect sizes of approximately 0.80 can be considered large, 0.5 as moderate, and 0.2 small [45]. Participant adherence to low-risk alcohol guidelines (by either abstaining or not exceeding recommended limits) was assessed in terms of percentages (yes/no).

If means and standard deviations were not reported, we contacted the study authors to obtain these and/or we used the procedures of the Comprehensive Meta-Analysis software (CMA, version 2.2.021) to calculate the effect size using continuous or dichotomous outcomes. In the event these were not available either, we used other statistics (such a t- or p-value). Where possible, data from intention-to-treat analyses were used; completers-only data were used if the former were unavailable. If more than one alcohol consumption outcome measure was reported in a single study, we averaged the effect sizes from those measures to produce a single summary effect size for use in the meta-analysis, statistically adjusting those calculations to account for variance introduced by the multiple measures [46].

We calculated the mean effect sizes using a random effects model. This assumes that the included studies were drawn from ‘populations’ of studies that systematically differed from one another (heterogeneity). As a test of homogeneity of effect sizes, we calculated the I² statistic, an indicator of heterogeneity in percentages. A value of 0% indicates no observed heterogeneity, and larger values show increasing heterogeneity, with 25% as low, 50% as moderate and 75% as high [47]. As the I² statistic is known to be imprecise [48], we calculated the 95% confidence interval using the non-central chi-squared-based approach within the heterogi module in Stata [49]. We also estimated numbers needed to treat (NNTs) [50].

We calculated both beforehand and afterwards how many studies would be needed to ensure sufficient statistical power to identify relevant effects as we expected a small to moderate effect size [26], [51]. The power calculations were carried out according to the procedures described by Borenstein and colleagues [46]. Beforehand we hoped to find enough studies to enable identification of a small effect size of d = 0.40 based on the random effects model. The power calculations indicated that this would require at least ten studies with a mean sample size of 70 participants per condition. That conservatively assumes a medium level of between-study variance (τ²), a statistical power of .80 and a significance level of α<.05.

To detect possible publication bias, we visually examined the funnel plots of the primary outcome measures for symmetry. We conducted Egger’s linear regression test of the intercept to quantify the bias captured by the funnel plot and test whether it was significant [52]. Duval and Tweedie trim-and-fill procedure was performed to further verify whether the pooled effect size estimate was unbiased [53]. These procedures were all performed with CMA.

A flowchart depicting our study selection procedure is shown in figure 1. In reporting the results we followed the guidelines of the PRISMA statement (see Checklist S1) [54].

Table 1 summarises the selected characteristics of the 16 studies (containing 23 comparisons) included in the meta-analysis. The studies assessed a total of 5,612 participants (3,268 in experimental and 2,344 in control conditions) and thus provided sufficient statistical power to detect a small effect size (see section 2.6).

In five studies, sample inclusion was based on self-reported alcohol consumption, using cut-off points indicative of alcohol use exceeding low-risk guidelines, with differing levels for men and women. Five other studies applied the Alcohol Use Identification Test (AUDIT [55]) or the Fast Alcohol Screening Test (FAST [56]). Two studies applied both AUDIT and alcohol consumption cut-off points; one selected on the basis of GGT (gamma-glutamyl transpeptidase) testing. Two of the sixteen studies [57], [58] included anyone interested in participating; for these studies, we confined our analysis to subgroups belonging to the at-risk drinking population.

Seven studies applied a single-focus therapeutic strategy, which in six cases was personalised normative feedback (PNF) and in one case a generic health education approach. The other nine studies used combined treatment approaches consisting of motivational interviewing (MI), personalised normative feedback (PNF), cognitive-behavioural therapy (CBT) and/or behavioural self-control and change principles. The control groups represented assessment-only (n = 6), waitlisted (n = 3) or alcohol information brochure conditions (n = 7). The outcome assessments to indicate alcohol consumption were expressed in terms of mean standard drinks per drinking day, total numbers of standard drinks in the previous week, mean standard drinks per drinking occasion or amounts of alcohol in grams.

The risk of bias varied among the studies (table 1), with 14 studies reporting adequate sequence generation, 6 reporting allocation to conditions by an independent party, 15 reporting blinding of outcome assessors or using self-report outcomes only, and 10 using intention-to-treat analyses. Dropout rates varied from 0% to 42%.

The effect of low-intensity Internet-based alcohol interventions to reduce alcohol consumption in comparison to controls was small but significant at post-test (g = 0.20, random effects model, 95% CI: 0.13–0.27, p<.001, NNT = 8.93). Results are shown in figure 2 (from high to low study effect sizes) and table 2. Heterogeneity was low but with a moderate confidence interval (I² = 27, 95% CI: 0–56). A post-hoc power calculation showed that our set of studies had sufficient statistical power (0.99) on the basis of the random effects model (with a low level of between-study variance, τ² = .001, and a significance level of α <.05).

Seven studies [37], [57]–[62] compared more than one group receiving differing types of Internet-based brief treatment with a single control group, so that our analysis included multiple comparisons from these studies. The fact that the comparisons were not independent of one another could have artificially reduced the heterogeneity of the analysed studies, thereby affecting the pooled effect size. To test this, we carried out sensitivity analyses that included only one effect size per study. As table 2 shows, removal of the comparisons with the highest effect sizes had almost no influence on the pooled effect size nor did removing the comparisons with the lowest effect sizes. Removal of the one guided intervention comparison with the highest effect size (in Blankers [37]) did not influence the observed effect size either, nor did removal of that with the lowest effect size [62].

On average, the intervention participants were drinking 2,2 alcohol consumptions (22 grams of ethanol) less per week at post-treatment than controls (n = 14; 95% CI: 0.87–3.46, p = .001, I² = 0, p<.001; mean difference). Post-test differences [37], [61], [63]–[65]) revealed that intervention participants were significantly more likely than controls to have reduced their alcohol consumption to within the low-risk guidelines as compared to controls (n = 6; RD 0.13, 95% CI: 0.09–0.17, p<.001, I² = 0, non-significant).

Subgroup analyses revealed no significant differences between study characteristics and effect sizes for alcohol consumption (see table 2). The differences between types of control conditions bordered on significance (p = .056). We found a higher effect size for decreased alcohol consumption for studies applying a waitlist control condition (g = 0.48) than those applying an alcohol brochure condition (g = 0.20) or an assessment-only condition (g = 0.15).

No significant differences in effect remained at follow-up (6 to 12 months after baseline) between the six unguided interventions (8 comparisons) and control groups (g = 0.06, 95% CI: −0.14–0.25, p = .567, random effects model) for which such follow-up assessments were available. No follow-up assessments were available for the guided interventions.

Meta-regression analyses with Hedges’s g as the dependent variable uncovered no significant associations between effect size and either the number of alcohol intervention sessions (β = −0.0001, 95% CI: −0.004–0.003, p = .938) or the risk of bias (β = 0.068, 95% CI: −0.15–0.01, p = .089) in the studies assessed.

There was evidence of publication bias in terms of Duval and Tweedie’s trim-and-fill method. After adjustment for missing studies, the effect size for decreased alcohol consumption diminished from g = 0.20 to g = 0.14 (95% CI: 0.06–0.22; trimmed studies n = 8, random effects model). Egger’s test indicated an asymmetric funnel plot (p = .028, two-tailed).

Results of the subgroup analyses did not reveal any significant differences between experimental and control conditions. All these results need to be interpreted with caution, as the number of studies included in the subgroup analyses was low. This means that there where either no real differences between these conditions or that real difference may have gone undetected. The variation in types of control predictors was of borderline significance (p = .056) in terms of effect. A moderate effect size was found for studies using waitlist control conditions, while those with assessment-only or alcohol brochure control showed small ones. Other studies have similarly reported higher effect sizes for intervention studies that used waitlisted groups as comparators [73]. One explanation could be that waitlisted participants tend to delay behavioural change because they anticipate professional help in the near future; that could cause overestimation of the intervention effect.

We did not find a significantly greater effect size for guided (g = 0.23) than for unguided (g = 0.20) alcohol interventions, even though such significant differences in benefit have been overwhelmingly established for web-based treatment of depression and anxiety [34], [74]. Our lack of significant effect might be due to the fact that many participants in web-based alcohol interventions are first-time help seekers; they may hence derive health gains from their first formal attempt at behavioural change, whether unguided or guided. Alternatively, a real difference may have gone undetected as a consequence of the low number of guided interventions in our analysis (5 comparisons. Only the Blankers and colleagues [37], and the Doumas and Hannah [57] studies provided direct comparisons between guided and unguided interventions. Both showed a small, but non significant, difference in effect in terms of alcohol consumption reduction in favour of guided interventions. These non-significant results are probably due to lack of power in both studies as well.

In contrast with our previous analysis from 2011 [26], we now found no significant differences in alcohol reduction between single-session interventions and more extended ones. Although the literature is somewhat inconclusive [75], it provides some confirmation for our current findings [30], [68], [76].

Web-based interventions may offer considerable promise for reducing alcohol misuse by women. We found no difference in alcohol consumption outcomes between all-male and mixed-gender samples, whereas several studies on face-to-face alcohol interventions in primary care had reported that men were more likely to benefit than women [30], [67]. In the case of Internet-based interventions for alcohol misuse, however, female uptake appears equally as high as male uptake [28], [77] and have been seen to have similar impacts on female and on male drinking, or possibly even greater influence on females, as suggested by Riper and colleagues (2008, [78]).

No difference in effect sizes emerged between studies that used cut-off points in alcohol consumption as study inclusion criteria and those that applied stricter measurements such as AUDIT [55]. AUDIT scores among the latter were high (averaging around 20, indicating a potentially high risk of alcohol dependence amongst participants. Internet interventions might thus well be effective for a broad spectrum of people who misuse alcohol. Just as in many trials of brief alcohol interventions and routine practice studies [18], [79], the studies in our analysis did not conduct diagnostic interviews to assess for alcohol dependence. This lack of actual diagnoses also hampers any attempt to use the available data to test the common view that self-help interventions are particularly suited to people with less serious alcohol problems, but less appropriate for those with alcohol dependence [3], [80].

Several limitations underlie our meta-analysis that may have affected our overall results. First, as indicated the number of studies included in the subgroup analyses was low. The resulting insufficient statistical power may call into question our outcomes whereby no significant difference between a number of conditions could be observed. Second, some included studies had substantial dropout rates (above 30%; see table 1). High study (and treatment) dropout rates are a common phenomenon in both online and offline self-help interventions for alcohol misuse and in Internet interventions in general [81], [82]. Third, the impact of online self-help in reducing alcohol consumption may have been underestimated here because control group drinking was also assessed; such assessment alone possibly motivates controls to reduce their consumption [83], [84]. Last but not least, we were not able to evaluate possible negative side-effects of Internet-based interventions for problem drinking, as the studies lack reports on such effects.

The results of this study support the use of guided and unguided Internet-based self-help interventions for curbing alcohol misuse in various settings (primary health care, work environments and the community). Although the overall effect size for these interventions was small, the public health impact could be substantial if large numbers of people who misuse alcohol were to take part in these interventions. Decreasing alcohol consumption as well as abstinence and adherence to low-risk guidelines are health benefits in their own right and potential predictors of longer-term maintenance of decreased alcohol consumption [85]. A modelling study by Smit and colleagues [86] has suggested that if online interventions were to partially replace conventional face-to-face brief alcohol interventions, that could sustain comparable levels of population health at lower costs.

Future studies should try to assess which type (s) of alcohol misuse populations could benefit most from brief online alcohol interventions. More studies with longer-term follow-up periods (over 12 months) are needed, too, to assess the maintenance of intervention effects over time in terms of reduced consumption and other health outcomes. Studies focusing on the effects of guided self-help interventions in curbing alcohol misuse, in direct comparison with unguided interventions, could shed light on whether the former produce better outcomes and, if so, at what costs. It is also important to investigate whether combining low-intensity Internet interventions with brief face-to-face interventions (blending of channels) would increase the effectiveness of interventions to curb alcohol misuse.