After initially successful quit attempts, many people return to smoking within a year, reducing the public health benefits of investment in smoking cessation. We aimed to assess whether interventions designed to prevent relapse after a successful quit attempt reduce the proportion of recent quitters who return to smoking.
We searched the Cochrane Tobacco Addiction Review Group trials' register. We selected randomized or quasi-randomized controlled trials of relapse prevention interventions with a minimum follow-up of 6 months. We included people who quit on their own, underwent enforced abstinence, or were in treatment programs. We included trials comparing relapse prevention interventions with no intervention or cessation plus relapse prevention with cessation intervention alone. Two of us independently extracted data from each report, with disagreements referred to a third author.
Forty-two studies met the inclusion criteria. The most common interventions were skills training to identify and resolve tempting situations and extended treatment contact. A few studies tested pharmacotherapy. We separately analyzed studies that randomized abstainers and those that randomized participants before their quit date. Within subgroups of trials, pooled odds ratios ranged from 0.86 to 1.30, and in most analyses, 95% confidence intervals included 1. Most studies had limited power to detect moderate differences between interventions.
The evidence to date does not support the adoption of skills training or other specific interventions to help individuals who have successfully quit smoking to avoid relapse, but this is an important area for future study.
Nicotine replacement,1 some antidepressants,2 and behavioral support3,4 for smoking cessation increase long-term quit rates compared with control, but a proportion of initially successful participants return to smoking over time. Several strategies for improving public health by reducing this proportion have been studied. These strategies include behavioral techniques, such as skills training,5 extended treatment contact, imaginary cue exposure, aversive smoking and social support, drug treatments, and other interventions primarily used for supporting quit attempts. In planning tobacco treatment programs, it is important to be informed about the relative effectiveness of different strategies, particularly in determining how much resource to allocate to helping quit attempts vs supporting abstinence. The objective of this review is to provide information to assist this decision. An extended version of this review has been published and will be regularly updated in the Cochrane Database of Systematic Reviews.6
We searched the Cochrane Tobacco Addiction Review Group register of trials, which includes the results of systematic searches, updated quarterly, of MEDLINE, PsycINFO, and conference abstracts. We identified studies mentioning relapse prevention or maintenance in the title, abstract, or keywords. The most recent search was in August 2005.
We included randomized or quasi-randomized controlled trials with at least 6 months of follow-up after quitting. We included participants who had quit smoking on their own, were in enforced abstinence, or were in cessation programs. There is no clear distinction between a relapse prevention intervention and an extended cessation treatment. Thus, we included interventions identified by study investigators as intended to prevent relapse, compared with no intervention, a shorter intervention, or an intervention not oriented toward relapse prevention. The outcome was abstinence at follow-up of at least 6 months from randomization.
We extracted data on study setting, population, method of randomization, and allocation concealment; age, sex, baseline cigarette consumption, and period of quitting of participants; interventions and control condition; outcome, including length of follow-up; definition of cessation; and validation of self-reported smoking status.
The primary outcome was the number of quitters at the longest follow-up. We used biochemically validated cessation in preference to self-report where available, preferring continuous or prolonged abstinence to point prevalence abstinence where possible. We classified randomized participants who withdrew, were lost to follow-up, or failed to provide validation samples as continuing smokers. When studies reported strict and more lenient outcomes, we extracted both and conducted a sensitivity analysis on the pooled results. We expressed individual study results as an odds ratio (OR) with a 95% confidence interval (CI) and pooled study outcomes using a fixed-effect (Mantel-Haenszel) model, unless there was significant statistical or clinical heterogeneity between trials. We separately analyzed trials that randomized abstainers from those that randomized smokers. We also separated studies in which contact time was matched and those in which the relapse prevention included longer contact.
We performed subgroup analyses for longer (>4 weeks) and shorter durations of intervention, in trials randomizing smokers to matched-duration interventions, and between more (>4 sessions) and fewer intervention sessions for unmatched intervention and control programs. We also considered subgroup analyses for “skills” and social support studies, and for spontaneous quitters such as pregnant women and individuals seeking smoking cessation treatment.
We identified 42 studies for inclusion. One article7 reported 2 trials each with multiple arms relevant to different comparisons, and 48- 11 included subgroups or factorial designs contributing to different comparisons. Two (5%) of the studies did not specifically describe the intervention as involving relapse prevention. One12 was a replication of an included study, and one13 randomized abstainers.
Twenty-six studies randomized people who had stopped smoking (Table 1). The interventions for preventing relapse included behavioral strategies and pharmacotherapy. Intensive behavioral interventions involved repeated face-to-face contact usually aiming at teaching clients to identify tempting situations and to apply a range of coping and cognitive strategies to resist relapse. Less intensive interventions included written materials and brief face-to-face or telephone contacts.
Among the studies randomizing people who had stopped smoking, 9 randomized pregnant14- 19 or postpostpartum20- 22 abstainers. Two studies9,13 randomized hospital inpatients with cardiovascular illness who had not smoked during hospital admission, and one23 randomized hospital patients who were abstinent on the day of discharge. Two studies24,25 randomized military recruits undergoing enforced abstinence. Five studies10,11,26- 28 randomized participants recruited from local communities.
Five studies29- 33 randomized abstainers who had taken part in a cessation program to behavioral interventions. Four studies randomized abstainers to pharmacological interventions, including nicotine chewing gum10,11 and bupropion hydrochloride.34,35
Seventeen studies (including 1 also contributing to the first category9) randomized smokers who then attempted to quit with or without relapse prevention components (Table 2).
In 9 studies, intervention and control conditions were matched for the amount of contact. Seven studies (1 with 2 components)7,8,36- 39 used a group behavioral format, and 29,40 used individual counseling. Three provided pharmacotherapy to all treatment participants (the studies by Emmons et al38 and Buchkremer et al [with 2 components]7). A factorial design tested nicotine gum against no gum.40
Most smoking cessation studies comparing more with less intensive treatments include some intervention to prevent relapse. We only included trials that specified relapse prevention as an explicit focus of the intervention. We did not include studies offering treatment proactively to special populations, such as pregnant or hospitalized smokers, because all trials using these groups provide some relapse prevention input within the active treatment arm, and they are covered in separate Cochrane reviews. Where studies had 3 or more treatment conditions, we compared the most with the least intensive interventions. Seven studies7,12,41- 45 compared longer with shorter programs, all involving face-to-face contact. The relative intensity of the cessation and the relapse prevention components varied. One study46 compared group-based behavior therapy for 8 weeks plus proactive calls 1, 8, and 11 months later with group therapy alone. We excluded other studies that tested the use of telephone counseling as an adjunct to nicotine replacement therapy, because most of the behavioral support was provided during the cessation period.
Many trials were small and had limited power to detect realistic differences in quit rates, especially in the group that randomized smokers before the quit date.
Studies randomizing successful end-of-treatment quitters provide the most straightforward test of relapse prevention interventions designed for clinical practice. All 4 studies10,11,34,35 of pharmacological treatments used this approach, but only 2 studies31,33 of behavioral treatments randomized participants who were abstinent for more than 1 week of treatment.
We required a report of smoking status a minimum of 6 months from the start of the intervention. In the case of studies that randomized smokers before quitting, this could have been from the quit date. Some studies timed follow-up from the end of treatment. Three trials9,22,38 reported 6 months of follow-up; all others had a longer follow-up. Some studies did not provide a definition of abstinence, and most others reported point prevalence rather than sustained abstinence.
All but 6 studies20,22,24,25,28,29 used some form of biochemical validation of self-reported smoking status, but in some other cases, samples were not collected from all participants, were not collected at long-term follow-up, or were not used to correct self-reports.
Four studies used cluster-randomized designs. In the 2 among military recruits,24,25 allocation was by training group and selection bias was unlikely. In the others, allocation was by midwife19 or pediatric practice,20 and selection bias in the subsequent enrollment of participants might have been possible. Two of the cluster-randomized trials reported that correlation between outcomes in individuals in the same cluster was small so that reporting individual outcomes was acceptable. These 2 trials also had high loss to follow-up, although there was no evidence of differential loss between arms.
In the absence of significant findings in meta-analysis subgroups, we did not attempt to explore the influence of study quality on outcomes.
We did not detect a significant benefit at the end of pregnancy from 6 trials14- 19 (n = 1183; OR, 1.17; 95% CI, 0.90-1.53). We also failed to detect an effect in the studies15,17- 22 that included postpartum follow-up (n = 2695; OR, 1.08; 95% CI, 0.92-1.27).
We failed to detect an effect of intervention in hospitalized patients who had not smoked in the hospital, based on 2 studies9,13 (n = 558; OR, 0.86; 95% CI, 0.60-1.22). One further study46 offering 3 telephone calls for relapse prevention among patients abstinent at discharge failed to detect evidence of benefit (n = 106; OR, 1.20; 95% CI, 0.57-2.64).
Neither trial24,25 detected a benefit of intervention. In both trials, the period of enforced abstinence gave rise to a higher quit rate than the spontaneous rate expected in these populations of young smokers, but no effect was detected from the additional interventions. Less than 3% of participants used the telephone support offered in one trial.25
We detected no evidence of a benefit of interventions to prevent relapse in people who had quit unaided10,11,26- 28 (n = 3561; OR, 1.14; 95% CI, 0.96-1.34). All 5 studies used self-help interventions, although in one,28 the materials were individually tailored based on information collected via telephone questionnaires. Using different comparator groups in the 2 factorial studies27,28 of different types of self-help did not substantially alter the pooled effect.
We detected no long-term effect of skills-based interventions to prevent relapse in 5 studies29- 33 in which abstaining smokers were randomized after participation in a formal treatment program (n = 1121; OR, 1.00; 95% CI, 0.80-1.25). This meta-analysis compared the most intensive intervention with the least intensive control in the trials with more than 2 arms. Using a different comparison did not change the conclusion.
Two trials10,11 detected a small effect of nicotine gum (n = 2261; OR, 1.30; 95% CI, 1.06-1.61). We failed to detect a significant benefit of bupropion when we pooled data from 2 trials34,35 (n = 605; OR, 1.25; 95% CI, 0.86-1.81).
We found no benefit from the use of specific relapse prevention components in group or individual format interventions, based on 9 trials (with 1 trial that included 2 components)7- 9,36- 40 (n = 793; OR, 0.91; 95% CI, 0.65-1.27). There was no evidence of heterogeneity. Because all but 140 of the studies involved treatment contact for more than 4 weeks, we did not conduct a subgroup analysis by treatment duration. Most trials used a skills training approach.
One study8 comparing different versions of a self-help program did not detect a difference in quit rates (OR, 1.71; 95% CI, 0.61-4.78).
We detected no effect of relapse prevention in 7 trials7,12,41- 45 involving extended face-to-face contact (n = 699; OR, 1.01; 95% CI, 0.71-1.44). We detected no significant heterogeneity.
One trial46 failed to detect a benefit of providing extended contact by telephone after an intensive 8-week group program (OR, 1.11; 95% CI, 0.86-1.43).
Through meta-analysis of randomized trials, we failed to detect a clinically significant effect of existing relapse prevention interventions in sustaining successful attempts to stop smoking. Because most studies concerned only 1 particular type of intervention (skills training), the volume of work is modest (to our knowledge, there exists only 1 study randomizing smokers at the end of a formal treatment period), and because many of the studies have serious limitations, there is a strong need for continuing research in this area.
Most studies included in this review evaluated low-intensity interventions, such as brief face-to-face encounters, written materials, mailings, and telephone contact. Although only a few included studies had adequate sample sizes to detect the expected effects, the CIs around the pooled estimates suggest that it is unlikely that the analysis failed to detect a significant benefit of low-intensity interventions. However, it is more difficult to exclude a clinically useful effect of more intensive interventions, because these have been less extensively studied.
Any negative verdict is limited to the only treatment approach studied extensively so far, the skills training approach. Other approaches, which have not been studied well or at all, have been proposed; these include opportunistic use of nicotine replacement, contingency contracting, social support, cue exposure (only imaginary exposure has been studied so far), and interventions aimed at maintaining abstainers' morale.
We included all studies that randomized abstainers, because these provide the best test of interventions aimed at maintaining abstinence. We also included studies randomizing smokers before quitting, which were described as tests of relapse prevention treatments, although there is not a clear-cut distinction between those interventions and others tested as pure cessation interventions.
There are 2 arguments in favor of randomizing smokers before stopping smoking. From a theoretical perspective, it may be difficult to separate cessation and relapse prevention advice; and from a practical perspective, sample sizes are usually much higher at the start than at the end of treatment. The methodological disadvantage of integrating cessation and relapse prevention is that it reduces power to detect specific relapse prevention effects. The primary outcome variable is normally the abstinence rate at follow-up. It is difficult to differentiate effects of the intervention on the initial smoking cessation from effects on preventing relapse in smokers who were initially successful. One solution to this problem is to provide a separate analysis of those achieving initial success. However, none of the existing studies used this approach, and it also poses problems with randomization if the initial cessation rate is unequal in the 2 groups.
Randomizing only those smokers who have made a successful quit attempt provides a stronger design for isolating the effects of relapse prevention, because true effects are not masked by other factors related to the initial success or skewed by uneven initial cessation rates. Of the existing studies using this approach, most recruited spontaneous abstainers, such as pregnant women. Of the studies of behavioral methods for relapse prevention, only 131 randomized smokers abstinent at the end of an initial treatment episode and 329,30,32 randomized smokers abstinent 5 to 8 days after their quit day.
The studies randomizing abstainers varied considerably in the periods for which participants had already abstained from smoking, from 24 hours to 16 months. This reflects the lack of a consistent definition of a successful quit attempt.
Future studies should consider randomizing smokers who were abstinent continuously and completely for at least 4 weeks, and use as the primary outcome measure continuous lapse-free abstinence of at least 6 months if the intervention was aimed at avoiding lapses. Where the intervention aimed at helping patients to cope with lapses should these occur, a period of grace (eg, 6 months) should be included, followed by another 6 months of lapse-free abstinence.
In summary, this review does not exclude a small effect of some relapse prevention interventions, but neither does it provide evidence to support inclusion of relapse prevention interventions in smoking treatment programs.
Correspondence: Tim Lancaster, MSc, MB, BS, Department of Primary Health Care, University of Oxford, Old Road Campus, Headington, Oxford OX3 7LF, England (firstname.lastname@example.org).
Accepted for Publication: September 16, 2005.
Author Contributions: Dr Lancaster had full access to all the data in the study and takes responsibility for the integrity of the data and the accuracy of the data analysis.
Financial Disclosure: None.
Funding/Support: The Cochrane Tobacco Addiction Review Group is supported by the National Health Service of the United Kingdom.
Role of the Sponsor: The funding body had no role in data extraction and analyses, in the writing of the manuscript, or in the decision to submit the manuscript for publication.
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