Motivational interviewing for substance abuse
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the effects of motivational interviewing, as a primary or support intervention, for substance abuse, in terms of levels of drug use and engagement in further treatment.
Background
Description of the condition
According to the World Health Organization (WHO 2009) there are 76.3 million persons with alcohol use disorders worldwide. In addition, there are at least 15.3 million persons who have drug use disorders, and injecting drug use is reported in 136 countries.
Substance abuse refers to the overindulgence in and dependence on a drug or other chemical leading to effects that are detrimental to the individual's physical and mental health, or the welfare of others. The disorder is characterized by a pattern of continued pathological use of a medication, non‐medically indicated drug or toxin, that results in repeated adverse social consequences related to drug use, such as failure to meet work, family, or school obligations, interpersonal conflicts, or legal problems. There are on‐going debates as to the exact distinctions between substance abuse and substance dependence. We follow the definitions by the American Psychiatric Association (APA 2000) and distinguish between the two by defining substance dependence in terms of physiological and behavioral symptoms of substance use, and substance abuse in terms of the social consequences of substance use. Substance abuse may lead to addiction or substance dependence. Medically, physiologic dependence requires the development of tolerance leading to withdrawal symptoms. Both abuse and dependence are distinct from addiction which involves a compulsion to continue using the substance despite the negative consequences, and may or may not involve chemical dependency (APA 2000). Dependence almost always implies abuse, but abuse frequently occurs without dependence, particularly when an individual first begins to abuse a substance. Dependence involves physiological processes while substance abuse reflects a complex interaction between the individual, the abused substance and society. There is also a distinction between "misuse" and "abuse" of substances. Substance misuse is the incorrect use of medication by patients, who may use a drug for a purpose other than that for which it was prescribed; or use of a substance for unintended purposes (APA 2000). The objective of this review is substance abuse, dependency or addiction, but not misuse.
Description of the intervention
Motivational interviewing (MI) was started by Miller (Miller 1983) and developed by Miller and Rollnick (Miller 1991). MI is a client‐centred, semi‐directive method for enhancing intrinsic motivation to change by exploring and resolving ambivalence. MI integrates the relationship‐building principles of Carl Rogers (Rogers 1951) with more active cognitive‐behavioural strategies. The intervention has four basic principles (described below). A brief variant of MI is called Motivational Enhancement Therapy (MET). MET is manual‐based, and was developed as part of Project MATCH (Project MATCH 1997) . Project MATCH was a large multi site trial comparing MI with cognitive behavioral therapy (CBT) and twelve‐step facilitation therapy. MI counselling does not require professional training as nurse, psychologist, etc. Hence, MI may be incorporated in programmes run by health care staff as well as e. g. prison staff. There are explicit standards for practitioners regarding education and competence, and there is a quality control to ensure that the method is in fact used as intended. One instrument for assessing treatment integrity is the Motivational Interviewing Treatment Integrity (MITI) scale (Moyers 2005). Promising results have been reported as to the effect of the method for alcohol dependence, smoking cessation, drug addiction, HIV‐risk behaviours, treatment adherence, diet & exercise, and eating disorders (Carey 2007); (Burke 2004 ; Hettema 2005; Rubak 2005). MI has recently been introduced into the criminal justice system, in Europe as well as in North‐America. In practice, MI has never been studied in its pure form. The research has employed adaption of MI (AMIs) in various forms (Burke 2003).
How the intervention might work
MI is supposed to work through its four main principles: (1) express empathy, (2) support self‐efficacy, (3) roll with resistance, and (4) develop discrepancy. As expressed on the official homepage of Motivational interviewing (http://motivationalinterview.org/clinical/principles.html), (1) involves seeing the world through the client's eyes. (2) means that clients are held responsible for choosing and carrying out actions to change. (3) means that the counsellor does not fight client resistance, but "rolls with it." Statements demonstrating resistance are not challenged. Instead the counsellor uses the client's "momentum" to further explore the client's views. (4) Motivation for change occurs when people perceive a discrepancy between where they are and where they want to be. MI counsellors work to develop this situation through helping clients examine the discrepancies between their current behavior and future goals. When clients perceive that their current behaviours are not leading toward some important future goal, they become more motivated to make important life changes. Apodaca and Longabaugh (Apodaca 2009) did a literature search to identify potential within‐session mechanisms of change in MI. The most consistent evidence was found for three constructs: client change talk/intention (related to better outcomes); client experience of discrepancy (related to better outcomes); and therapist MI‐inconsistent behavior (related to worse outcomes).
Why it is important to do this review
The intervention is used widely, and therefore it is important to find out whether it helps, harms or is ineffective. Several reviews and meta‐analyses have been published (e.g. Andreasson 2003; Burke 2003; Burke 2004; Carey 2007; deWildt 2002; Dunn 2001; Emmelkamp 2006; Grenard 2006; Hettema 2005; Larimer 2007; Nahom 2005; Rubak 2005; Vasilaki 2006 ) but they all differ somewhat from our review. Some of them have studied effects of MI (AMI) on other groups in addition to substance abusers or studied only alcohol abusers. Others included other interventions than MI. Still others included other designs than randomised trials. The main strength of the review being proposed by this protocol is that it employs a comprehensive and systematic search strategy aiming to be exhaustive. We will also assess the methodological quality of the included studies and grade the evidence for the primary outcomes.
Objectives
To assess the effects of motivational interviewing, as a primary or support intervention, for substance abuse, in terms of levels of drug use and engagement in further treatment.
Methods
Criteria for considering studies for this review
Types of studies
We include studies where units (persons, therapists, institutions) were allocated randomly or quasi‐randomly to motivational interviewing or other conditions. Included studied must be published in or after 1983, which was the year that MI was introduced. Because most psychosocial interventions have many unspecific elements in common, and because terms like "motivational intervention" and motivational interview" not necessarily refers to Miller's specific program of MI, we include only studies that reviewed audio or video recordings to ensure that the intervention given was indeed MI. There is no limitation on length of study. Qualitative studies will not be included in this review.
Types of participants
Persons defined as having either substance abuse, dependency or addiction, but not misuse. There are no limitations on age or other participant characteristics. The term substance refers to a drug of abuse, a medication, a toxin or alcohol, excluding nicotine. The reason for excluding nicotine, is because there is an existing protocol on motivational interviewing for smoking cessation (Douglas 2008). According to International classification of Diseases version 10 (ICD‐10) (WHO 1993) this includes the following codes, F10 to F19, excluding F17 (tobacco)*. Equivalent disorders and codes in the Diagnostic and Statistical Manual of Mental Disorders, third revised edition (DSM‐III‐R) (APA 1987) and fourth edition, (DSM‐IV) (APA 1994), chapter Substance‐Related disorders, will also be included. We also include studies in which substance abuse is not formally diagnosed. Participants could be dual diagnosis clients. We include both participants who only abuse substances and participants who also have mental problems, but we analyse the two groups separately.
*[Mental and behavioural disorders due to use of ‐ alcohol (F10 ‐ 303.‐), ‐ opioids (F11), ‐ cannabinoids (F12), ‐ sedatives or hypnotics (F13), ‐ cocaine (F14), ‐ other stimulants (amphetamine) (F15), ‐ hallucinogens (F16), ‐ volatile solvents (F18) and ‐ multiple drug use and use of other psychoactive substances (F19).]
Types of interventions
Experimental intervention
Primarily, the interventions should be labelled motivational interviewing or motivational enhancement therapy. The intervention could basically be offered in three ways: (1) as a stand‐alone therapy, (2) MI integrated with another therapy, or (3) MI as a prelude to another therapy (e.g. cognitive behavioral therapy).
We will include studies where MI or MET is used alone, as a prelude to other therapy or integrated with other therapy. We include individual, face‐to‐face interventions. We exclude group interventions, and interventions not given in person (e.g. computer‐delivered or telephone interventions).
Studies must include audio‐ or videotaping of sessions in order to assess fidelity of treatment.
Control intervention
The comparator could be no intervention, waiting list control, placebo psychotherapy or other active therapy.
Types of outcome measures
Data on substance abuse may be both dichotomous (number of participants ceasing substance abuse) and continuous (e.g. mean number of days used in last 30 days. Substance abuse may also be measured using various scales or inventories like the OTI (Opiate Treatment Index) (Darke 1991; Darke 1992), the Timeline Follow‐Back (Sobell 1992), and the Rutgers Alcohol Problems Index (RAPI; White 1989).
Primary outcomes
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cease of substance use measured by self‐report, report by collaterals, urine analysis, or blood samples et
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reduction in substance abuse measured as above.
Outcomes will typically be recorded as a posttest immediately after the interventions ended, short‐term follow‐ups until six months after the intervention ended, medium‐term follow‐ups of between six and 12 months, and long‐term follow‐ups of more than 12 months. The exact follow‐up durations will be recorded for each study.
Secondary outcomes
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Number of repeat convictions (for convicted substance abusers).
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Enhance retention and engagement in treatment.
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Improve motivation for change, e.g. measured by the Readiness to Change Questionnaire (RCQ; Heather 1993).
Search methods for identification of studies
Electronic searches
We will search the following electronic databases: Medline, Embase, PsycInfo, PsychExtra, Cochrane Central Register of Controlled Trials, C2‐SPECTR, International Bibliography of the Social Sciences (IBSS), Sociological Abstracts, Web of Science (ISI), SveMed+, CINCH, NCJRS, SpringerLink, Wiley Interscience, DrugScope Library, Electronic Library of the National Documentation Centre on Drug Use, Google Scholar, and Google. Year of publication is limited to 1983 and later.
Databases will be searched using a strategy developed incorporating the filter for the identification of RCTs (Higgins 2008) combined with selected MeSH terms and free text terms relating to substance abuse. The MEDLINE search strategy will be translated into the other databases using the appropriate controlled vocabulary as applicable. The search strategy for MEDLINE is shown in Appendix 1.
We will search the following web sites and mailing lists:
Websites:
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www.motivationalinterview.org
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http://nrepp.samhsa.gov/programfulldetails.asp?PROGRAM_ID=182
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http://www.controlled‐trials.com
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http://clinicalstudyresults.org
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http://centrewatch.com
Mailinglists:
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MINT‐listserv; a mailing list available to members of MINT (Motivational Interviewing Network of Trainers)
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Australian Criminology Listserv
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Campbell Crime&justice group steering committee
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Crimnet. http://www.law.usyd.edu.au/mailman/listinfo/crimnet.
Searching other resources
We will make contact with MI developers, practitioners and independent researchers to identify unpublished reports and ongoing studies. References in obtained reviews and included primary studies will be scanned to identify new leads.
Data collection and analysis
Dealing with dependent data
When there are more than one intervention group that are compared with a single control group, we will not include both comparisons in the same meta‐analysis. When there are several follow‐up times, we will analyse them separately. When there are more than one measure of the same outcome, we will use the standardised mean value.
Selection of studies
References from the searches will be uploaded into SRS 4.0 software for screening and data extraction. The screening will proceed in 4 levels. At Level 1, two reviewers will scan the titles of each reference. Each reviewer scores either "promote to next level", "exclude" or "can't tell". Only if both reviewers score "exclude" will the reference be excluded. If at least one reviewer scores "can't tell" or "include", the reference is promoted to Level 2. At Level 2, the titles and abstracts are read, and the same promotion rules apply. References promoted to Level 3 are ordered in full text. Two reviewers read the full texts and score "include" or "exclude". If there is disagreement, and the two reviewers cannot agree, a third reviewer decides whether to include the study.
Data extraction and management
At level 4, data from each study are extracted by two reviewers using the data extraction form. The same rules for tackling disagreement as at Level 3 apply. If outcome or other vital information is missing from the original reports, we will contact the corresponding author by e‐mail in an attempt to retrieve the necessary data for the analysis.
Assessment of risk of bias in included studies
The risk of bias assessment for RCTs and CCTs in this review will be performed using the six criteria recommended by the Cochrane Handbook (Higgins 2008). The recommended approach for assessing risk of bias in studies included in Cochrane Reviews is a two‐part tool, addressing six specific domains (namely sequence generation, allocation concealment, blinding, incomplete outcome data, selective outcome reporting, and other issues). The first part of the tool involves describing what was reported to have happened in the study. The second part of the tool involves assigning a judgement relating to the risk of bias for that entry. This is achieved by answering a pre‐specified question about the adequacy of the study in relation to the entry, such that a judgement of "Yes" indicates low risk of bias, "No" indicates high risk of bias, and "Unclear" indicates unclear or unknown risk of bias. To make these judgments we will use the criteria indicated by the handbook adapted to the addiction field. See Table 1 for details.
| Item | Judgment | Description | |
| 1 | Was the method of randomisation adequate? | yes | The investigators describe a random component in the sequence generation process such as: random number table; computer random number generator; coin tossing; shuffling cards or envelopes; throwing dice; drawing of lots; minimization |
| no | The investigators describe a non‐random component in the sequence generation process such as: odd or even date of birth; date (or day) of admission; hospital or clinic record number; alternation; judgement of the clinician; results of a laboratory test or a series of tests; availability of the intervention | ||
| unclear | Insufficient information about the sequence generation process to permit judgement of ‘Yes’ or ‘No’. | ||
| 2 | Was the treatment allocation concealed? | yes | Investigators enrolling participants could not foresee assignment because one of the following, or an equivalent method, was used to conceal allocation: central allocation (including telephone, web‐based, and pharmacy‐controlled, randomisation); sequentially numbered drug containers of identical appearance; sequentially numbered, opaque, sealed envelopes |
| no | Investigators enrolling participants could possibly foresee assignments because one of the following method was used: open random allocation schedule (e.g. a list of random numbers); assignment envelopes without appropriate safeguards (e.g. if envelopes were unsealed or non opaque or not sequentially numbered); alternation or rotation; date of birth; case record number; any other explicitly unconcealed procedure. | ||
| unclear | Insufficient information to permit judgement of ‘Yes’ or ‘No’. This is usually the case if the method of concealment is not described or not described in sufficient detail to allow a definite judgement | ||
| 3 | Was knowledge of the allocated interventions adequately prevented during the study? (blinding of patients, provider, outcome assessor) Objective outcomes | yes | Blinding of participants, providers and outcome assessor and unlikely that the blinding could have been broken; Either participants or providers were not blinded, but outcome assessment was blinded and the non‐blinding of others unlikely to introduce bias. No blinding, but the objective outcome measurement are not likely to be influenced by lack of blinding |
| 4 | Was knowledge of the allocated interventions adequately prevented during the study? (blinding of patients, provider, outcome assessor) Subjective outcomes | yes | Blinding of participants, providers and outcome assessor and unlikely that the blinding could have been broken; Either participants or providers were not blinded, but outcome assessment was blinded and the non‐blinding of others unlikely to introduce bias. |
| no | No blinding or incomplete blinding, and the outcome or outcome measurement is likely to be influenced by lack of blinding; Blinding of key study participants and personnel attempted, but likely that the blinding could have been broken; Either participants or outcome assessor were not blinded, and the non‐blinding of others likely to introduce bias | ||
| unclear | Insufficient information to permit judgement of ‘Yes’ or ‘No’ | ||
| 5 | Were incomplete outcome data adequately addressed? For all outcomes except retention in treatment or drop out | yes | No missing outcome data; Reasons for missing outcome data unlikely to be related to true outcome (for survival data, censoring unlikely to be introducing bias); Missing outcome data balanced in numbers across intervention groups, with similar reasons for missing data across groups; For dichotomous outcome data, the proportion of missing outcomes compared with observed event risk not enough to have a clinically relevant impact on the intervention effect estimate; For continuous outcome data, plausible effect size (difference in means or standardized difference in means) among missing outcomes not enough to have a clinically relevant impact on observed effect size; Missing data have been imputed using appropriate methods All randomised patients are reported/analysed in the group they were allocated to by randomisation irrespective of non‐compliance and co‐interventions (intention to treat) |
| no | Reason for missing outcome data likely to be related to true outcome, with either imbalance in numbers or reasons for missing data across intervention groups; For dichotomous outcome data, the proportion of missing outcomes compared with observed event risk enough to induce clinically relevant bias in intervention effect estimate; For continuous outcome data, plausible effect size (difference in means or standardized difference in means) among missing outcomes enough to induce clinically relevant bias in observed effect size; ‘As‐treated’ analysis done with substantial departure of the intervention received from that assigned at randomisation; | ||
| unclear | Insufficient reporting of attrition/exclusions to permit judgement of ‘Yes’ or ‘No’ (e.g. number randomised not stated, no reasons for missing data provided; number of drop out not reported for each group); |
The domains of sequence generation and allocation concealment (avoidance of selection bias) will be addressed in the tool by a single entry for each study.
Blinding of participants, personnel and outcome assessor (avoidance of performance bias and detection bias) will be considered separately for objective outcomes (e.g. drop out, use of substance of abuse measured by urine‐analysis, subjects relapsed at the end of follow up, subjects engaged in further treatments) and subjective outcomes (e.g. duration and severity of signs and symptoms of withdrawal, patient self‐reported use of substance, side effects, social functioning such as integration at school or at work, family relationship).
Incomplete outcome data (avoidance of attrition bias) will be considered for all outcomes except for the drop out from the treatment, which is very often the primary outcome measure in trials on addiction. It will be assessed separately for results at the end of the study period and for results at follow up.
Control of initial difference in prognostic factors between groups
In a properly randomised study, all initial differences between groups will be caused by chance. This applies to all prognostic variables, both known and unknown. But some times randomisation fail, and there may be important initial differences between groups. These differences can be systematic, and they can appear in unmeasured variables as well as in the measured ones. It is generally possible to control for the latter but not the former. Matching can be used before the intervention to make groups more similar, and regression methods can be used after the intervention to control for initial differences, but all these methods may introduce bias in the results (Deeks 2003). We use this question to judge whether randomisation was successful. Studies in which both generation and concealment of allocation sequence are MET, will be coded as MET below.
MET = Control for one or more prognostic factors. Also score MET when there is no control for prognostic factors because there was no imbalance in measured variables.
UNCLEAR = Sufficient information could not be obtained.
NOT MET = Imbalance in prognostic factors and failure to control for this imbalance.
Grading of evidence
The quality of evidence will be assessed according to a systematic and explicit method (Guyatt 2008). In order to indicate the extent to which one can be content that an estimate of effect is correct, judgments about the quality of evidence will be made for each comparison and outcome. These judgments consider study design (RCT, quasi RCT or observational study), study quality (detailed study design and execution), consistency of results (similarity of estimates of effect across studies) and directness (the extent to which people, interventions and outcome measures are similar to those of interest). The following definitions 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. Moderate: further research is likely to have an important impact on our confidence in the estimate of effect and may change the estimate. Low: further research is very likely to have an important impact on our confidence in the estimate of effect and may change the estimate.
Very low: any estimate of effect is very uncertain.
Measures of treatment effect
We will compare the treatment and control groups for outcomes at post‐test and at different follow‐up times. For dichotomous data, we will report relative risks (risk ratios). For continuous data we will report standardised mean differences. 95 percent confidence intervals will be used as measures of the amount of random errors influencing the outcome estimations. We will use the optimal information size (OIS) (Pogue 1997) for assessing whether there is a sufficient sample size for concluding that there is a statistically significant effect in a meta‐analysis. Using a two‐sided alpha of 0.01 and power of 0.95 we calculate that a total sample size of 1,786 is necessary for detecting a small standardised mean difference (SMD). For SMDs of 0.5 (medium) and 0.8 (large), the OIS are 290 and 116, respectively.
Unit of analysis issues
In cluster‐randomised trials, the elements are groups of individuals (e.g. prisons, geographical areas, clinics), rather than individuals themselves. In such studies, care should be taken to avoid unit‐of‐analysis errors. If there for instance are a total of 100 substance abusers with 25 abusers in each of four clinics, and two clinics are randomised to receive the intervention and the other two are randomised to receive the control, the correct N to use in the analysis is not 100 but smaller. The effective sample size of a single intervention group in a cluster‐randomised 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 randomised controlled trials in this review, we try 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). But the ICC is seldom reported in the primary studies. The number of participants can be used in the analyses if the ICC is used as a correcting factor. For dichotomous data both the number of participants and the number experiencing the event can be divided by the same design effect (Green 2008).
Dealing with missing data
We will contact authors by email to collect missing data. Statisticians often use the terms ‘missing at random’, and ‘not missing at random’ to represent different scenarios. Data are said to be ‘missing at random’ if the fact that they are missing is unrelated to actual values of the missing data. Data are said to be ‘not missing at random’ if the fact that they are missing is related to the actual missing data. In cases where we assume that data is missing at random, we will analyse only the available data. If we assume that the data are not missing at random, we will Impute the missing data with replacement values, and treat these as if they were observed. We will do this in different ways and compare the results (e.g. last observation carried forward, imputing an assumed outcome such as assuming all were poor outcomes, imputing the mean, imputing based on predicted values from a regression analysis).
Assessment of heterogeneity
Statistically significant heterogeneity among primary outcome studies will be assessed with Chi‐squared (Q) test and I‐squared (Higgins 2003). A significant Q ( P<.05) and I‐squared of at least 50% will be considered as statistical heterogeneity.
Assessment of reporting biases
We will use funnel plots for information about possible publication bias. But 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.
Data synthesis
If meta‐analyses are performed, we will report both fixed‐effect and random effects meta‐analyses. If meta‐analyses are not judged to be appropriate, we will report the results for each individual study.
Subgroup analysis and investigation of heterogeneity
We will investigate the following factors with the aim of explaining observed heterogeneity: fidelity check, type of substance, intensity or length/period of the intervention, profession of therapist, characteristics of the control condition, quality and application of measurement tools, and differences in participant characteristics (e.g. whether they have a formal diagnosis of substance abuse or not). We will also compare results for studies with or without the developers of MI William R. Miller or Stephen Rollnick on the author list or mentioned as mentors or trainers. We will analyse effects separately for MI alone, MI integrated with other therapy, and MI given as a prelude to other therapy.
If there are many primary studies, we classify them according to these variables in order to identify possible sources of heterogeneity. We will consider performing moderator analyses (stratification on subgroups, meta‐analysis analogue to ANOVA, meta‐regression) to explore how observed variables are related to heterogeneity.
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. By limiting the studies to be included to those with higher quality, we will examine if the results change, and check for the robustness of the observed findings. 1. Quasi‐randomised studies versus randomised studies. 2. Excluding trials whose drop out rate is greater than 20%. 3. Performing the worst case scenario ITT (all the participants in the experimental group experience the negative outcome and all those allocated to the comparison group experience the positive outcome) and the best case scenario ITT (all the participants in the experimental group experience the positive outcome and all those allocated to the comparison group experience the negative outcome).
| Item | Judgment | Description | |
| 1 | Was the method of randomisation adequate? | yes | The investigators describe a random component in the sequence generation process such as: random number table; computer random number generator; coin tossing; shuffling cards or envelopes; throwing dice; drawing of lots; minimization |
| no | The investigators describe a non‐random component in the sequence generation process such as: odd or even date of birth; date (or day) of admission; hospital or clinic record number; alternation; judgement of the clinician; results of a laboratory test or a series of tests; availability of the intervention | ||
| unclear | Insufficient information about the sequence generation process to permit judgement of ‘Yes’ or ‘No’. | ||
| 2 | Was the treatment allocation concealed? | yes | Investigators enrolling participants could not foresee assignment because one of the following, or an equivalent method, was used to conceal allocation: central allocation (including telephone, web‐based, and pharmacy‐controlled, randomisation); sequentially numbered drug containers of identical appearance; sequentially numbered, opaque, sealed envelopes |
| no | Investigators enrolling participants could possibly foresee assignments because one of the following method was used: open random allocation schedule (e.g. a list of random numbers); assignment envelopes without appropriate safeguards (e.g. if envelopes were unsealed or non opaque or not sequentially numbered); alternation or rotation; date of birth; case record number; any other explicitly unconcealed procedure. | ||
| unclear | Insufficient information to permit judgement of ‘Yes’ or ‘No’. This is usually the case if the method of concealment is not described or not described in sufficient detail to allow a definite judgement | ||
| 3 | Was knowledge of the allocated interventions adequately prevented during the study? (blinding of patients, provider, outcome assessor) Objective outcomes | yes | Blinding of participants, providers and outcome assessor and unlikely that the blinding could have been broken; Either participants or providers were not blinded, but outcome assessment was blinded and the non‐blinding of others unlikely to introduce bias. No blinding, but the objective outcome measurement are not likely to be influenced by lack of blinding |
| 4 | Was knowledge of the allocated interventions adequately prevented during the study? (blinding of patients, provider, outcome assessor) Subjective outcomes | yes | Blinding of participants, providers and outcome assessor and unlikely that the blinding could have been broken; Either participants or providers were not blinded, but outcome assessment was blinded and the non‐blinding of others unlikely to introduce bias. |
| no | No blinding or incomplete blinding, and the outcome or outcome measurement is likely to be influenced by lack of blinding; Blinding of key study participants and personnel attempted, but likely that the blinding could have been broken; Either participants or outcome assessor were not blinded, and the non‐blinding of others likely to introduce bias | ||
| unclear | Insufficient information to permit judgement of ‘Yes’ or ‘No’ | ||
| 5 | Were incomplete outcome data adequately addressed? For all outcomes except retention in treatment or drop out | yes | No missing outcome data; Reasons for missing outcome data unlikely to be related to true outcome (for survival data, censoring unlikely to be introducing bias); Missing outcome data balanced in numbers across intervention groups, with similar reasons for missing data across groups; For dichotomous outcome data, the proportion of missing outcomes compared with observed event risk not enough to have a clinically relevant impact on the intervention effect estimate; For continuous outcome data, plausible effect size (difference in means or standardized difference in means) among missing outcomes not enough to have a clinically relevant impact on observed effect size; Missing data have been imputed using appropriate methods All randomised patients are reported/analysed in the group they were allocated to by randomisation irrespective of non‐compliance and co‐interventions (intention to treat) |
| no | Reason for missing outcome data likely to be related to true outcome, with either imbalance in numbers or reasons for missing data across intervention groups; For dichotomous outcome data, the proportion of missing outcomes compared with observed event risk enough to induce clinically relevant bias in intervention effect estimate; For continuous outcome data, plausible effect size (difference in means or standardized difference in means) among missing outcomes enough to induce clinically relevant bias in observed effect size; ‘As‐treated’ analysis done with substantial departure of the intervention received from that assigned at randomisation; | ||
| unclear | Insufficient reporting of attrition/exclusions to permit judgement of ‘Yes’ or ‘No’ (e.g. number randomised not stated, no reasons for missing data provided; number of drop out not reported for each group); |
