PROTOCOL: Effect of early,brief computerized interventions on risky alcohol use and risky cannabis use among young people: protocol for a systematic review

Trends and consequences of alcohol misuse amongst young people

Alcohol misuse presents a substantial societal burden due to the costs related to health care, prevention, crime, law enforcement and welfare assistance, as well as the costs resulting from reduced productivity and increased mortality (Thavorncharoensap, Teerawattananon, Yothasamut, Lertpitakpong, & Chaikledkaew, 2009).

The WHO Global Survey on Alcohol and Health (2008) found a trend towards increased drinking among young people aged 18-25 years over the last five years, with an 80 percent increase in risky alcohol consumption in the participating countries (WHO, 2011).

Risky and harmful drinking patterns such as binge drinking and drinking to intoxication have also increased over time among young people (Editorial Lancet, 2008; The National Center on Addiction and Substance Abuse at Columbia University, 2007).

Small to moderate levels of alcohol might not be harmful, but high consumption of alcohol is directly related to risky behaviours such as intoxicated driving (Cherpitel, Ye, Bond, & Borges, 2003) and interpersonal violence (Foran & O'Leary, 2012). In addition, binge drinking can have both short- and long-term negative impacts on an individual's health. Lopez-Caneda et al. (2013), for instance, found an association between binge drinking and anomalous neural activity related to working memory processes, and college students who binge drink have been shown to have a higher risk of developing alcohol dependence in later years (Jennison, 2004).

Trends and consequences of cannabis use amongst young people

Cannabis is the most widely used and trafficked illicit drug worldwide (United Nations Office on Drugs and Crime, 2012). Cannabis is a general term to describe the psychoactive preparations of the plant Cannabis sativa. While marijuana refers to the cannabis leaves or other crude plant material, the term hashish describes the drug produced by drying the resin exuded by the marijuana plant (Brecher, 1972). Cannabis is commonly smoked, with or without being mixed with tobacco – but can also be consumed orally.

The United Nations Office on Drugs and Crime (UNODC) has estimated that between 2.9 to 4.3 percent of the world population aged 15-64 (between 129 and 191 million people) used cannabis at least once in 2008 (United Nations Office on Drugs and Crime, 2010a). Whereas the use of inhalants (defined as substances producing chemical vapours such as found in beauty products like hairspray) is more commonly used among young people and might decline with age, the use of marijuana and hashish increases with age (Mosher, Rotolo, Phillips, Krupski, & Stark, 2004). Cannabis use has increased in the U.S. since 2007 in the 13 to 18 year age group and daily marijuana use reached a 30-year peak among high school students aged 17-18 years in 2011 (Johnston, O'Malley, Bachman, & Schulenberg, 2012).

Regular cannabis use among young people presents a social burden due to costs arising from increased health care use and a higher risk for school-drop out. Although there appears to be no standard measure for ‘low’ or ‘high’ frequencies of cannabis use, we define ‘high users of cannabis’ according to the literature as users with at least weekly consumption of the drug (Lev-Ran, Le Foll, McKenzie, George, & Rehm, 2013). It has been reported that regular cannabis use among young people may have a negative impact on their cognitive functioning (Ramaekers, Berghaus, van Laar, & Drummer, 2004; Ramaekers et al., 2006), and on the developing brain (Pope, Grubera, Hudsona, Cohanea, & Yurgelun-Toddb, 2003). The current literature suggests a positive association between frequency of cannabis use and the risk of developing a mental illness, especially psychotic disorders (Løberg et al., 2012). On the other hand, there is some evidence that cannabis use can have a positive impact on creativity (Schafer et al., 2012), and is helpful in the treatment of

certain ailments such as cancer (Robson, 2001) and multiple sclerosis (Iskedjiana, Berezaa, Gordonc, Piwkoa, & Einarsona, 2007).

Other risk factors including unprotected sexual behaviour and risky driving behaviour have been found to be associated with increased use of alcohol (Jennison, 2004; Karam, Kypri, & Salamoun, 2007; J. Miller, Naimi, Brewer, & Jones, 2007) and of cannabis (Anderson & Stein, 2011; Hall & Degenhardt, 2009). In addition, the development of substance abuse disorders in later life has been found associated with the use of alcohol (Odgers et al., 2008) and cannabis (Behrendt, Wittchen, Hofler, Lieb, & Beesdo, 2009) during youth. Thus, there is a need for early interventions to reduce or eliminate the use of alcohol and cannabis among young people in order to prevent them from falling into a downward spiral that may lead to substance abuse related behaviours and ailments in adulthood.

Impact of potential moderators that might amplify the effect of brief, computerized interventions for certain subgroups

Gender and education might influence the effect of brief, computerized interventions. For example, males and young adults with higher education use digital media more than females and young adults with lower education (OECD, 2008). These two groups may therefore be more likely to benefit from computerized interventions because their past experience is likely to have led to more efficient use of digital media.

3.1.1 Types of studies

We will include studies where units (e.g., persons, therapists, institutions) are allocated randomly or quasi-randomly to an early, brief computerized intervention and at least one other comparator condition. Both efficacy studies (where the treatment is studied under ideal conditions) and effectiveness studies (where the treatment is studied under real-world conditions) will be included. We will include studies where early, brief computerized interventions are used as a stand-alone treatment. Eligible comparators include no intervention, waiting list control or alternative brief intervention, which may be computerized or delivered face-to-face.

The studies included in the review will be randomized controlled trials:

RCTs – randomized controlled trials where participants are randomly allocated to intervention and control group(s) by, for example, drawing lots or automatic algorithms.

We will exclude studies using non-randomised procedures for allocation (such as self-selection).

3.1.2 Types of participants

The review will include studies in which the participants are young people between 15 and 25 years of age who are high or risky consumers of alcohol or cannabis, or both. We will include studies of university students and of senior high school students even if no further information on age is provided. We will exclude studies that state only that the participants were young.

High or risky consumption of alcohol is defined as either (a) consuming at least five (for males) or four (for females) drinks during any one drinking session, or (b) consuming more than fourteen (for males) or more than seven (for females) drinks a week (National Institute on Alcohol Abuse and Alcoholism, 2013). In the US, a standard drink is defined as one which contains about 0.6 fluid ounces or 14 grams of ‘pure’ alcohol.

High or risky consumption of cannabis is defined in different ways; whereas some scholars view risky consumption of cannabis as daily or near-daily use (Fischer et al., 2011), others use a broader definition to include those who consume cannabis at least once a week (Webb, Ashton, Kelly, & Kamali, 1996). In this review, we define risky cannabis use among young people as the frequent consumption of cannabis at least once a week.

Existing studies on the effect of brief computerized interventions on risky drug use have usually defined young people in a range 15 to 25 years (Bingham et al., 2010; Voogt et al., 2011; Voogt et al., 2012), and we have limited our target group accordingly. If we find studies comprising interventions to reduce the use of other types of substances simultaneously (e.g. cocaine), we will exclude them unless they analyse results on risky alcohol or cannabis use separately. If the study includes young people over 25 years of age, the mean age should be 25 years or less. If the study includes young people under 15, the mean age should be not be less than 15 years. The definition of ‘young people’ might vary in different countries and cultures. In addition, the debut age for using alcohol and cannabis is assumed to vary between different countries.

3.1.3 Types of interventions

For the purposes of this review, we define ‘early intervention’ as being delivered at an early stage of substance use (an ‘indicated prevention’). An ‘indicated preventive strategy’ targets individuals at high-risk who have been identified as having minimal but detectable signs foreshadowing alcohol and cannabis abuse (O'Connell, Boat, & Warner, 2009). Early, brief computerized interventions appear to be an important tool to stop the development of severe alcohol and cannabis use among young people at risk.

This review will include all types of early, brief computerized interventions regardless of medium, provider or theoretical framework. These may be ‘automatic only’ or delivered with the involvement of trained real-time ‘counselors’ (e.g., social workers, psychologists, or other health care workers). Automatic interventions and interventions with trained real-time counselors will be analyzed separately. Studies with booster sessions will be included but analyzed separately.

This review will only include ‘brief’ interventions defined as any preventive or therapeutic activity (such as is delivered by a health worker, psychologist, or volunteer worker) given within a maximum four structured therapy sessions, each of short duration (W. Miller et al., 1992) that typically lasts between five and ten minutes with a maximum total time in treatment of one hour (Babor, 1994).

3.1.4 Types of comparators

The comparator condition can be: an alternative early, brief intervention, no intervention or waiting list control.

Examples of comparisons are:

Early, brief computerized intervention (e.g. electronic screening and brief intervention) vs. non-computerized early brief intervention (treatment as usual, e.g. face to face screening and feedback)

3.1.5 Types of outcomes

Primary outcome:

Alcohol use, measured by validated scales (e.g. the Daily Drinking Questionnaire; Collins, Parks, and Marlatt (1985); the Alcohol Timeline Followback [TLFB]; Sobell, Brown, Leo, and Sobell (1996) or by self-report

We will compare changes in use (e.g. frequency, quantity or peak consumption, occasions, drinking days) between intervention and comparators at baseline and at all follow-ups. Alcohol use and cannabis use will be analyzed separately.

Secondary outcomes:

Motivation for change, measured using a validated instrument (e.g. Readiness to Change Questionnaire [RCQ]; Heather, Rollnick, and Bell (1993).

Adverse outcomes:

Any reported adverse outcomes

We will examine outcomes at the following time points:

post-test (immediately after the interventions ends);

The exact duration of follow-up will be recorded for each study.

3.2.1 Electronic searches

Electronic searches will be made of bibliographic databases, as well as on open websites and in the grey literature. We will also search for on-going studies. There will be no publication, geographic, or language restrictions. The following sources will be searched:

MEDLINE

3.2.2 Search terms

Search terms for MEDLINE (modified as necessary for other databases) will be as follows: 1

exp computer systems/

3.2.3 Searching other resources

We will search for on-going studies in ClinicalTrials.gov and will contact experts in the fields to identify unpublished reports, on-going studies and studies that were not retrieved in the bibliographic search. We will conduct a hand-search of the tables of contents of the Journal of Consulting & Clinical Psychology for the years 2012 to present and will search all conference proceedings from INEBRIA (International Network on Brief Interventions for Alcohol & Other Drugs). Finally, we will examine the reference lists of included studies and relevant systematic reviews in the field.

3.3.1 Dealing with dependent data

3.3.2 Selection of studies

The screening of studies will proceed in two phases. At Level 1, two review authors will scan the title and abstract of each reference and score either “promote to next level”, “exclude”, or “can't tell”. Only if both review authors score “exclude” will the reference be excluded at this Level. If at least one review author scores ”can't tell” or “include”, the reference will be promoted to Level 2. References promoted to Level 2 will be ordered in full text and the same screening criteria will then be applied. Two review authors will read the full texts and score “include” or ”exclude”. If there is disagreement, a third review author will decide whether to include the study. We will not calculate the inter-rater reliability of individual coders' ratings, but we will pilot a small number of references and discuss the screening practices as a group in order to develop high agreement between raters before we screen the rest of the studies.

3.3.3 Data extraction and management

Data from each study will be extracted by two review authors using a specifically developed data extraction form (see Appendix 8.2) to record detailed information about authors, institutions, journal, participants, intervention, control conditions, research design, sample size, outcomes and results. We will apply the same rules for dealing with disagreement as described under 3.3.2.

3.3.4 Assessment of risk of bias in included studies

Two review authors will independently rate each selected study on the following risk of bias (RoB) domains developed by the Cochrane Collaboration (Higgins & Green, 2011). Uncertainty or disagreement will be resolved by discussion with a third review author.

Random sequence generation: ○

Low RoB: Resulting sequences are unpredictable (explicitly stated use of either computer-generated random numbers, table of random numbers, drawing lots or envelopes, coin tossing, shuffling, cards or throwing dice).

In a properly randomized study, all initial differences between groups will arise by chance. This applies to all prognostic variables, both known and unknown. In non-randomized designs, however, there may be important initial differences between groups. These differences can be systematic, and can appear in unmeasured variables as well as in the measured ones. It is generally possible to control for measured variables but not for unmeasured ones. Regression methods can be used after the intervention to control for initial differences, but such methods may introduce bias in the results (Deeks et al., 2003).

Studies, in which both generation and concealment of allocation sequence have a low RoB will be coded as low RoB below:

○

Low RoB: Control for one or more prognostic factors. Also score low RoB when there is no control for prognostic factors because there was no imbalance in measured variables.

Blinding of participants may only be possible in studies where those in the control condition receive an alternative intervention. If blinding is not possible, we will code this as high risk of bias.

Blinding of Personnel ○

Low RoB: Personnel unaware of the treatment given.

Blinding of personnel will be impossible for those who deliver treatment. In studies where there are no personnel involved and the intervention is totally automatic, the risk of bias in this domain will be coded as low.

Blinding of Assessor ○

Low RoB: Assessor unaware of the assigned treatment when collecting outcome measures. Also score as met if outcome is questionnaire data or register data.

We will code the risk of bias as low for studies of computerized interventions where data is recorded automatically.

Incomplete outcome reporting ○

Low RoB: Losses to follow up less than or equal to 20 % and equally distributed between comparison groups, and reasons for losses to follow up given, intention to treat analysis performed.

3.3.5 Grading of evidence

We will assess the quality of evidence using a systematic and explicit method, the Grades of Recommendation, Assessment, Development, and Evaluation” (GRADE) approach (Guyatt, Oxman, Schunemann, Tugwell, & Knottneru, 2011). We will make judgments about the quality of evidence for each comparison and outcome to indicate the extent to which it is possible to be content that an estimate of effect is correct. These judgments consider study design, study quality (detailed study design and execution), consistency of results (similarity of estimates of effect across studies), directness (e.g., the extent to which people, interventions and outcome measures are similar to those of interest), precision, publication bias, large effect, plausible confounding and dose-response gradient. The following categories in grading the quality of evidence for each outcome will be used:

High: Further research is very unlikely to change our confidence in the estimate of effect.

3.3.6 Measures of treatment effect

We will compare the outcomes of treatment and control groups at post-test and at short-, medium- and long-term follow-up. For dichotomous data, we will report relative risks (risk ratios), and for continuous data, we will report standardised mean differences. We will use 95 percent confidence intervals as measures of the random error influencing the outcome estimations. We will use the optimal information size (OIS; Poque and Yusuf (1997)) to assess whether the sample size is sufficient for concluding that there is a statistically significant overall effect in a meta-analysis. Using a two-sided alpha of 0.05 and power of 0.95 we calculate that a total sample size of 1,302 is necessary for detecting a small standardised mean difference (SMD) of 0.2. For SMDs of 0.5 (medium) and 0.8 (large), the OIS are 212 and 84, respectively.

3.3.7 Unit of analysis measure

In cluster-randomized trials one has to be careful to avoid unit-of analysis errors. The following may serve as an example: If the population of the study consists of a total of 100 risky alcohol users, distributed in four schools with 25 in each school, and two schools are randomized to the intervention and the other two to the control, the correct N to use in the analyses is not 100, but smaller. The effective sample size of a single intervention group in a cluster randomized trial is its original sample size divided by a quantity called the design effect. A common design effect is usually assumed across intervention groups. The design effect is 1 + (m - 1)r, where m is the average cluster size and r is the intra-cluster correlation coefficient (ICC). If we include any cluster randomized controlled trials in this review, we will attempt to measure the intra-cluster correlation. The total variance in the outcome can be partitioned into variance between groups (VBG) and variance within groups (VWG). The intra-cluster correlation is calculated as VBG/ (VBG+VWG). The number of participants can be used in the analyses if the ICC is used as a correcting factor; however, the ICC is seldom reported in primary studies. For dichotomous data both the number of participants and the number experiencing the event can be divided by the same design effect (Higgins & Green, 2011). If the ICC is not reported in primary cluster randomised studies we will consult a statistician for advice.

3.3.8 Dealing with missing data

Where not available from the published reports, we will contact authors by email to request any missing data or the reasons for missing data to allow a judgement to be made on whether these are ‘missing at random’ or ‘not missing at random’.

Data will be considered ‘missing at random’ if the reason for absence is judged as unrelated to actual values of the missing data. In contrast, data will be considered ‘not missing at random’ if the reason for absence is judged as related to the actual missing data.

Where data are not missing at random, we will analyse only the available data. Where data are missing at random, we will seek the advice of a statistician and will impute the missing data with replacement values, and treat these, as if they were observed. The method of imputation will be clarified after consulting a statistician.

Effect sizes will be calculated from means, standard deviations and N. Where these are not reported in sufficient detail, we will contact the authors of the primary studies. If this is unsuccessful, we will attempt to retrieve effect size data from published meta-analyses, or to calculate effect sizes using RevMan or CMA software from information such as t-values. If these strategies are unsuccessful, we will attempt to use the method described in Section 16.1.3 of the Cochrane Handbook (Higgins & Green, 2011). If means but not SDs are provided, we will consider imputing SDs from other similar studies.

3.3.9 Assessment of heterogeneity

We will assess for heterogeneity among primary outcome studies using the I² and τ² statistics (Higgins & Green, 2011) and will discuss any observed heterogeneity and its magnitude.

3.3.10 Assessment of reporting biases

We will use funnel plots to provide information about possible publication bias if there are more than ten included studies. We are aware, however, that asymmetric funnel plots are not necessarily caused by publication bias (and publication bias does not necessarily cause asymmetry in a funnel plot). If asymmetry is present, likely reasons will be explored.

Further, we will search for pre-published trial protocols and will compare the published report with its corresponding protocol where this is available.

3.4.1 Subgroup analysis and investigation of heterogeneity

We will investigate the following factors, where available, with the aim of explaining any observed heterogeneity:

differences in participant characteristics such as gender, education, age, setting, and readiness to change at baseline.

We will also investigate the effect of baseline frequency of use/dose.

We will analyse effects separately for studies including targeted feedback only, and for studies, including both, targeted and tailored feedback.

The studies will be analysed separately for the different time points.

If there are sufficient primary studies, we will classify them according to these variables in attempt to identify possible sources of heterogeneity. We will consider performing moderator analyses (e.g., stratification on subgroups, meta-analysis analogue to ANOVA, meta-regression) to explore how observed variables are related to heterogeneity.

3.4.2 Sensitivity analysis

If the number of included studies is sufficient (more than 10) we will assess the impact of differing methodological quality by sensitivity analyses. The following sensitivity analyses are planned a priori: 1.

Quasi-randomized studies versus randomized studies.

We will check for the robustness of the observed findings by examining the effect of limiting the studies to be included to those with low RoB.

Meta-analyses will be performed in RevMan, but we will consider conducting meta-regression in Comprehensive Meta-Analysis if the number of studies is sufficient.