Preventing the Onset of Depressive Disorders: A Meta-Analytic Review of Psychological Interventions

We began by conducting a comprehensive literature search in bibliographic databases for relevant articles published from 1966 to June 2007. We examined a total of 3,833 abstracts in PubMed (N=1,205), PsycInfo (N=1,146), EMBASE (N=313), and the Cochrane Central Register of Controlled Trials (N=1,169). In order to find unpublished studies, we also examined abstracts from Digital Dissertations (N=23). We searched these databases by combining terms indicative of prevention and depression (specifying searches for both MeSH terms and text words), while limiting the search to effect studies (randomized trials, controlled trials, clinical trials). Second, we examined the references of earlier reviews and meta-analyses (14 – 20), and we reviewed the reference lists of retrieved articles.

We included studies that used a pretest-posttest randomized controlled design and examined the effects of a preventive intervention on the incidence of new cases of depressive disorders compared with a control group that did not receive the intervention. To be included, studies had to use a standardized diagnostic interview at baseline to exclude the pretest presence of a full-blown depressive disorder and to examine the incidence of depressive disorders at follow-up. We also included studies that examined interventions aimed at reducing depressive disorders as a consequence of specific events (e.g., postnatal depression, poststroke depression) and did not have a pretest assessment of depressive disorders but did have a posttest assessment. Studies were excluded if they explicitly reported having included subjects with depressive disorders who then received the intervention. No limits were imposed on study publication language.

Although at least 25 scales are available to assess the validity and quality of randomized controlled trials (21), there is no evidence that they provide reliable assessments of validity. We therefore preferred to use a simple approach for assessing the validity of the studies, as suggested in the Cochrane Handbook (21), using three basic criteria: allocation to conditions by an independent (third) party; blinding of assessors of outcomes; and completeness of follow-up data. We did not use the fourth basic criterion described in the Handbook (adequacy of random allocation concealment to respondents), because it is inapplicable to studies comparing psychological interventions to no-treatment control groups.

Because the follow-up period of the studies varied considerably, we based the calculation of incidence rates on person-years. That is, we divided the number of new cases of depressive disorders that occurred during the follow-up period (the numerator) by the total person-time units (person-years) of the group at risk (the denominator). Technically, this is known as the person-time incidence rate or the incidence density rate. The person-time incidence rate is an appropriate measure of incidence when follow-up times are unequal (22) . In two studies, this method could not be used because the number of subjects was larger than the number of person-years as a result of the brevity of the follow-up period and the relatively large number of new cases during this period. For example, when 12 persons are studied for 3 months, they generate 4 person-years. If more than four persons develop a disorder during the follow-up period, the person-years incidence rate cannot be calculated. To solve this problem, we rescaled person-years into person-quarters (3 months), then combined the study outcomes meta-analytically, and finally back-transformed the outcome into incidence rates based on person-years. For each study, we calculated the incidence rate ratio as the incidence rate of developing a depressive disorder in experimental subjects relative to the incidence rate in control subjects.

To calculate pooled mean incidence rate ratios, we used the Comprehensive Meta-Analysis software package, version 2.2.021 (Biostat, Englewood, N.J.). Because we expected considerable heterogeneity, we conducted all analyses using the random-effects model (21), which assumes that the included studies are drawn from “populations” of studies that differ from each other systematically (thus exhibiting heterogeneity). In this model, the effect sizes resulting from included studies differ because of the random error within studies, but also because of true variation in effect size from one study to the next.

Because our analyses were based on the assumption of an underlying constant hazards model in both groups, which is not necessarily the case, we conducted several additional analyses. First, we calculated the odds ratio for each study (ignoring the differences in follow-up period between the studies) and pooled them. Second, we calculated the absolute risk differences for each study (again ignoring the differences in follow-up period); these risk differences were also pooled. Then we calculated the number needed to treat, which denotes how many people would have to receive a preventive intervention for one new case of depression to be prevented. The number needed to treat was calculated as the inverse of the absolute risk difference.

We also conducted a cumulative meta-analysis, in which the results of each new study were added to the total of the studies that had been conducted previously (23) . This method allows a determination of the point in time when the overall results of the studies became significant.

In our analyses, we tested whether there were genuine differences underlying the results of the studies (heterogeneity) or whether the variation in findings was compatible with chance alone (homogeneity) (24) . As an indicator of homogeneity, we calculated the Q statistic. A significant Q rejects the null hypothesis of homogeneity and indicates that the variability among the effect sizes is greater than what is likely to have resulted from subject-level sample error alone. We also calculated I ², which is an indicator of heterogeneity (in percentages) not accounted for by sample error. A value of 0% indicates no observed heterogeneity, and larger values show increasing heterogeneity, with 25% considered low, 50% moderate, and 75% high heterogeneity, suggesting that systematic factors are responsible for differences across the effect sizes of the primary studies (24) .

Subgroup and metaregression analyses were conducted according to the procedures implemented in the Comprehensive Meta-Analysis software. We used mixed-effects analyses, which pooled studies within subgroups with the random-effects model but tested for significant differences between subgroups with the fixed-effects model.

Publication bias was tested by inspecting the funnel plot on the primary outcome measure (incidence rate ratio) and by Duval and Tweedie’s trim-and-fill procedure (25), which yields an estimate of the effect size after the publication bias has been taken into account (again, as implemented in the Comprehensive Meta-Analysis program).

We retrieved a total of 135 articles that potentially met our inclusion criteria. Of these, 116 were excluded, 81 because the presence of depressive disorders was not assessed with a formal diagnostic interview, 13 because they were treatment and not prevention studies, 17 because they did not examine psychological interventions, and five for other reasons (articles that described the design of studies without results or articles with insufficient data).

A total of 19 studies (26 – 44) met all inclusion criteria; because one of these studies used three different preventive interventions and a control group, a total of 21 comparisons could be made between a preventive intervention group and a control group. The total number of respondents in the studies was 5,806 (3,014 in the intervention conditions and 2,792 in the control conditions). Selected characteristics of the included studies are presented in Table 1 .

Seven of the 19 studies were designed to prevent postpartum depression, four dealt with prevention in school settings, two were aimed at patients with a physical disorder, two focused on primary care patients, and the remaining studies were aimed at other target groups. Seven studies focused on adolescents, and 12 targeted adults (one focusing on older adults). In 14 studies, subjects with a diagnosed depressive disorder at baseline were excluded, while the interventions in the remaining five studies (aimed at high-risk groups) did not assess the presence of a depressive disorder at baseline. Of the 14 studies in which subjects with a diagnosed depressive disorder at baseline were excluded, 12 excluded those with a current depressive disorder and two excluded those who had a depressive disorder in the previous 6 months.

We distinguished three types of prevention (45) : universal prevention, such as school programs and mass media campaigns, aimed at the general population or segments of the general population, regardless of whether they have a higher-than-average risk of developing a disorder; selective prevention, aimed at individuals in high-risk groups who have not yet developed a mental disorder; and indicated prevention, aimed at individuals who have some symptoms of a mental disorder but do not meet diagnostic criteria. Two of the 21 contrast groups we included in our meta-analysis examined universal prevention, 11 examined selective prevention, and eight examined indicated prevention. Fifteen interventions were cognitive-behavioral therapy (CBT), three were interpersonal psychotherapy, and the remaining were other types of intervention (one-session debriefing; problem-solving; and mutual support). In 18 comparisons, a group format was used, and the remaining three comparisons used an individual format. The number of sessions ranged from one to 15.

The follow-up periods in the different studies ranged from 3 to 36 months. Ten studies were conducted in the United States, four in Australia, two in the United Kingdom, two in the Netherlands, and one in Serbia.

Although the quality of the included studies was relatively high, the criteria assessing the validity of the studies did not indicate very positive results. Only seven studies reported allocation to conditions by an independent party. Blinding of assessors of outcomes was reported in eight of the 19 studies. Dropout rates ranged from 1% to 41%. In nine studies, intention-to-treat analyses were conducted.

The mean incidence rate ratio for all 21 comparisons from the 19 studies was 0.78 (95% confidence interval [CI]=0.65–0.93), which was significant (p<0.01). Heterogeneity was low to moderate (Q=29.77, p<0.10; I ² =32.81%). The results of this meta-analysis are summarized in Table 2 and Figure 1 . The cumulative meta-analysis showed that the overall results became significant after the first four studies had been published in 2000 ( Figure 1 ).

Because the weight of one study (36) was very high (34.2%), and because this was also the study in which a very different type of intervention was used (one-session debriefing after childbirth), we examined whether removal of this study from the analysis would change the overall results. The resulting mean incidence rate ratio was 0.74 (95% CI=0.61–0.90, p<0.01), with low heterogeneity (Q=25.69, n.s.; I ² =26.05%), which is comparable to the incidence rate ratio found in the analyses with the full sample.

In one large study (39), three intervention conditions were compared with one control group. Because these three comparisons were not independent from each other, we examined whether removal of these comparisons would increase heterogeneity. The resulting mean incidence rate ratio was 0.74 (95% CI=0.59–0.92, p<0.01; Q=28.79, p<0.05; I ² =40.95%).

Neither the funnel plots nor Duval and Tweedie’s trim-and-fill procedure suggested a significant publication bias. The incidence rate ratio did not change after adjustment for possible publication bias (the observed and adjusted effect sizes were the same).

Our analyses were based on the assumption of an underlying constant hazards model in both groups, which may not be the case. We conducted several sensitivity analyses. We calculated the odds ratio for each study (ignoring the differences in follow-up period between the studies) and pooled them. The resulting odds ratio was 0.76 (95% CI=0.62–0.94; z=–2.59, p=0.01), which was comparable to the earlier analyses.

We also calculated the absolute risk differences for each study (again ignoring the differences in follow-up period). This resulted in a pooled risk difference of –0.045 (95% CI=–0.073 to –0.016, p<0.01), which corresponds to a number needed to treat of 22 ( Table 2 ). The numbers needed to treat for each study are presented in Figure 1 .

Because some heterogeneity was observed, we conducted a series of subgroup and metaregression analyses. The results of the subgroup analyses are presented in Table 2 . We examined whether the incidence rate ratio differed according to type of prevention (universal, selective, or indicated), target group (postpartum depression, students, or other), and age group (adolescents or adults). We also examined whether the studies in which subjects with a depressive disorder were excluded at baseline differed significantly from those in which high-risk groups were included without the exclusion of diagnosed cases. Then we examined whether type of intervention (CBT, interpersonal psychotherapy, or other) and format of the intervention (group or individual) were related to the incidence rate ratio.

As indicated in Table 2, the incidence rate ratio differed significantly in only one subgroup. Studies in which interpersonal psychotherapy was used as an intervention appeared to be significantly more effective than those in which CBT or other interventions were used. Given the small number of comparisons (N=3) examining interpersonal psychotherapy, however, these results should be interpreted with caution.

In most of the subgroup analyses, heterogeneity was low or low to moderate. The subgroups of studies using CBT interventions or interpersonal psychotherapy showed no evidence of heterogeneity. Studies using other interventions had moderate to high heterogeneity, as might have been expected.

We conducted the same subgroup analyses based on the risk differences. As indicated in Table 2, the type of intervention was again found to be associated with significant differences between subgroups. However, in these analyses, we also found that the different types of prevention (universal, selective, or indicated) differed significantly from each other (p<0.01).

Because universal prevention appeared to differ significantly from selective and indicated preventions, and prevention based on interpersonal psychotherapy differed significantly from the preventions used in the other studies, we conducted another subgroup analysis in which we excluded the two comparisons based on universal prevention and the three comparisons based on interpersonal psychotherapy. The resulting incidence rate ratio was 0.82 (95% CI=0.70–0.98, p<0.05; Q=18.28, n.s.; I ² =17.92%), and the risk difference in this subgroup of studies was –0.035 (95% CI=–0.063 to –0.007, p<0.05; Q=18.93, n.s.; I ² =20.74%). The pooled odds ratio (in which we ignored the differences in follow-up period between the studies) was 0.81 (95% CI=0.67–0.98, p<0.05).

We conducted a metaregression analysis to examine the relationship between incidence rate ratio and follow-up period. We found that the follow-up period was inversely related to the incidence rate ratio, although the association did not reach statistical significance (p<0.10; the point estimate of the slope was –0.023; 95% CI=–0.050 to 0.004). This result can be interpreted as an indication that the effects of the intervention become smaller over longer follow-up periods, which may indicate that the preventive interventions delay the onset of disorders rather than preventing them altogether. We also conducted a metaregression analysis to examine whether the incidence rate ratio was related to the number of sessions used in the preventive intervention, but no significant relationship was found.