Smoking contributes to many of the health problems leading to hospitalisation, particularly vascular disease, respiratory illness and many cancers. In addition, smoking increases the risk associated with hospitalisations for surgical procedures. Hospitalisation, especially for a tobacco-related illness, may boost receptivity to smoking cessation messages by increasing perceived vulnerability, a so-called 'teachable moment'. Illness also brings smokers to the healthcare setting, where they have contact with health professionals who can provide a smoking cessation message or intervention. In addition, procedures such as coronary arteriography that provide detail of the patient's cardiac status may minimise subsequent denial of cardiac risk by the patient (Ockene 1992). Many hospitals restrict or prohibit smoking by patients to protect patients and staff from secondhand smoke exposure. This smoke-free environment may also provide an opportunity for smokers to try out tobacco abstinence away from the usual environmental cues to smoke. For these reasons, providing (or at least initiating) tobacco dependence treatments in hospitals may be an effective preventive health strategy.
A number of studies have evaluated smoking cessation services provided or initiated in hospital. The interventions have included behavioural counselling of different forms and intensity (including post-hospitalisation contacts), pharmacological therapies (such as nicotine replacement therapy [NRT], bupropion and varenicline), and combinations of counselling and pharmacotherapy. The aim of this review is to evaluate the effectiveness of smoking cessation interventions initiated during a hospital stay. In order to inform policy, we aimed to identify the components of effective programmes. In addition, we aimed to explore whether there is a difference in effect according to the reason for hospitalisation or whether the effect holds for patients with a variety of admission diagnoses, and whether the effect of interventions in acute care hospitals is also observed in rehabilitation hospitals.
The primary objective was to determine the efficacy of any type of smoking cessation programme for hospitalised patients. Our hypotheses were that:
- Systematic behavioural intervention (brief advice, individual counselling, provision of self-help materials, group therapy) increases quit rates more than usual care, and intensive intervention increases quit rates more than brief intervention.
- Interventions that occur both in hospital and after discharge increase quit rates more than interventions limited to the hospital stay, and longer post-discharge follow-up increases quit rates more than short follow-up.
- Adding pharmacotherapy (such as NRT, bupropion or varenicline) to a behavioural intervention increases quit rates more than placebo or no medication, and combining pharmacotherapy with a behavioural intervention increases quit rates more than either alone.
A secondary objective was to explore the possibility that the efficacy of interventions differed for patients with different diagnoses. This was done using subgroup analysis of trials that recruited patients from more than one specialty, and by indirect comparison of trials that recruited patients from within one disease category. The primary review focuses on interventions for smokers who are admitted to an acute care hospital. Studies of interventions for smokers in rehabilitation hospitals have now been published. This update includes a new separate review of the efficacy of smoking interventions initiated during a stay in a rehabilitation hospital.
Criteria for considering studies for this review
Types of studies
Randomized or quasi-randomized controlled trials.
Types of participants
Participants were patients who were hospitalised and who were currently smoking (defined as having smoked within one month of hospital admission) or had recently quit (defined as having quit more than one month before hospital admission). We excluded trials of secondary prevention or cardiac rehabilitation that did not recruit on the basis of smoking history, and trials in patients hospitalised in facilities that primarily treated psychiatric disorders or substance abuse (including inpatient tobacco addiction programmes). We included interventions that began in either acute care hospitals or rehabilitation hospitals. We included trials that recruited all hospitalised smokers and those limited to patients who planned to quit smoking after hospital discharge. Trials in which 'recent quitters' were classified as smokers were included, but a sensitivity analysis was performed on these data to determine whether they differed from trials that excluded such individuals.
Types of interventions
Any intervention that was initiated during hospitalisation and that aimed to increase motivation to quit, to assist a quit attempt, or to help recent quitters avoid relapse was included. Interventions that began in hospital and continued after discharge were included. The intervention could be delivered by physicians, nursing staff, psychologists, smoking cessation counsellors or other hospital staff. The intervention could include advice, more intensive behavioural therapy, or smoking cessation pharmacotherapy, with or without continued contact after hospital discharge. The control intervention could be any less intensive intervention, such as brief advice to quit, or it could be usual care. Studies that provided identical treatment consisting of more than usual or minimal care during the hospital stay and then randomly assigned participants to different post-discharge interventions were analysed separately in a sensitivity analysis. We included studies of smoking interventions that were part of a broader risk reduction or rehabilitation programme only if it was possible to extract data on the outcome effects of the smoking cessation component specifically, and if details of the nature of the intervention and control were explicitly stated. We included studies that reported the use of NRT, bupropion, varenicline, or other pharmacotherapy for smoking cessation.
We categorised behavioural interventions during the hospital stay according to whether they included follow-up after discharge. Within these categories we further defined both the hospital and follow-up interventions by level of intensity. This led to four categories of intervention intensity:
1. Single contact in hospital lasting <= 15 minutes, no follow-up support.
2. One or more contacts in hospital lasting in total > 15 minutes, no follow-up support.
3. Any hospital contact plus follow-up <=1 month.
4. Any hospital contact plus follow-up > 1 month.
Types of outcome measures
The principal outcome measure was abstinence from smoking at least six months after the start of the intervention. We used the most conservative measure of quitting at the longest follow-up, i.e. we preferred a biochemically validated quit rate to self-reported abstinence, and preferred continuous or sustained abstinence to point prevalence abstinence. We used abstinence at 12-month follow-up in preference to abstinence at six-month follow-up. We counted participants lost to follow-up as continuing smokers.
Search methods for identification of studies
We searched the Tobacco Addiction Group trials register in December 2011. This specialised register is regularly updated by electronic searches of databases including CENTRAL (2011 Issue 4), MEDLINE (via OVID to update 20111104.ud), EMBASE (via Ovid to update 20111104.em), PsycINFO (via OVID to 2011 November week 4) and handsearching of conference abstracts. Searches for the register cover smoking cessation, nicotine dependence, nicotine addiction and tobacco use. To identify papers potentially relevant to this reivew we searched for (hospital and patient*) or hospitali* or inpatient* or admission* or admitted in the title or abstract. In addition, we searched CINAHL (EBSCO to March 2012, search strategy in Appendix 1). We searched the Centers for Disease Control Smoking and Health database for the original review but since it did not retrieve any additional studies we did not use it for the update. We asked individuals with expertise in the area of smoking cessation for details of conference abstracts and studies in press. We hand-checked bibliographies of studies generated by the search for further studies.
Data collection and analysis
Identification of studies and data extraction
Three authors checked studies identified by the search strategies for relevance. Two authors extracted data independently. Disagreements were resolved by consensus. We noted reasons for the exclusion of studies. For each study we extracted the following data:
(i) author(s) and year of publication,
(ii) methods (country of origin, recruitment, randomization and participants),
(iii) description of intervention(s) and control, including a designation of intensity for behavioural interventions (1-4),
(iv) outcomes (length of follow-up, definition of abstinence, validation technique).
If necessary we contacted the original authors for clarification of data.
We reported the following information about each trial in the Characteristics of included studies table:
- Reasons for hospitalisation or specialty of admission
- Criteria for recruitment (e.g. current smokers only or recent quitters) and whether selected according to willingness to make a quit attempt
- Method of randomization and adequacy of concealment
- Smoking behaviour and characteristics of participants
- Therapist types
- Description of experimental and control interventions and classification by length of in-hospital contact and post-discharge support
- Outcome measures (definition of abstinence used in review, use of biochemical validation), number of deaths.
Assessment of risk of bias in included studies
We judged risk of bias on the basis descriptions of the randomization and allocation concealment procedure, as this is the main source of bias which has been empirically associated with over-estimation of treatment effects (Schulz 1995). We also assessed whether the studies reported validation of self-reported smoking cessation, and assessed the studies for attrition bias, including how they handled patients lost to follow-up, since these are possible sources of bias in smoking cessation studies. We also assessed the extent to which study populations consisted of current smokers and recent quitters.
Analysis of the data
We used statistical methods for pooling using a Mantel-Haenszel fixed-effect method, with 95% confidence intervals. This summary statistic replaced the Peto method (Yusuf 1985) used in earlier versions of this review, since the Mantel-Haenszel method is now recommended for Cochrane reviews (Higgins 2011). Differences in results using the two methods are small, and most likely to be apparent where numbers are unbalanced between groups, in which case the Peto method may give biased results. Where there was substantial heterogeneity between studies we explored possible reasons using sensitivity analyses or considered the impact of outliers. We express results as a risk ratio (intervention risks/control risks) for achieving abstinence from smoking together with the 95% confidence interval for this estimate. To investigate statistical heterogeneity we used the I² statistic, given by the formula [(Q - df)/Q] x 100%, where Q is the Chi² statistic and df is its degrees of freedom (Higgins 2003). This describes the percentage of the variability in effect estimates that is due to heterogeneity rather than sampling error (chance). A value greater than 50% may be considered to indicate moderate to substantial heterogeneity.
We calculated quit rates based on the numbers of patients randomized to an intervention, excluding any deaths. Those who dropped out or were lost to follow-up were counted as continuing smokers. Most studies verified self-reported smoking status with a biochemical test. In these studies, self-reported nonsmokers who did not pass the verification procedure were counted as smokers. We noted the number of deaths in Characteristics of included studies.
We analysed data according to our pre-determined classification of four levels of intensity (see Types of interventions, above). Where we included studies that were judged to be more prone to bias, we planned sensitivity analyses to assess whether their inclusion altered our findings. We also planned sensitivity analyses to explore, where possible, the contribution of different components to an overall effect (for example, the role of NRT in a multicomponent intervention) and to determine whether the effects were different when the study population was restricted to those wishing to stop. Another sensitivity analysis explored the efficacy of interventions that differed only after hospital discharge. In these studies participants received an identical intervention in the hospital and were randomly assigned to different post-discharge treatments.
In an exploratory analysis, we evaluated the effects of interventions in patients admitted to hospital because of the following diagnoses: cardiovascular disease, respiratory disease and cancer. We also assessed the effects of interventions that were designed to be delivered to all (or nearly all) of the smokers who were admitted to hospital regardless of the smoker's admitting diagnosis. Where there were insufficient data for meta-analysis, the results were tabulated. In cases where a single study reported data on patients from different categories, we pooled the data only when it was possible to extract data by disease category. Otherwise we included only those studies reporting data from patients in a single disease category. A separate analysis included studies that met inclusion criteria but were conducted in rehabilitation hospitals rather than acute care hospitals. These studies were not included in the main analysis.
We include the Tobacco Addiction Group glossary of tobacco-specific terms (Appendix 2).
Description of studies
Fifty trials conducted in the United States, the United Kingdom, Australia, Belgium, Brazil, Canada, Denmark, Germany, Israel, Japan, the Netherlands, Norway, and Spain between 1990 and 2011 met the inclusion criteria and contributed to the review. The previous version of this review included 33 trials published between 1990 and 2007; this update includes 17 new studies. All but 12 of the 50 studies contributed to the main comparison of a behavioural counselling intervention, classified by intensity, versus control. Eight that did not contribute (Campbell 1991; Campbell 1996; Ortega 2011; Rigotti 2006; Planer 2011; Simon 2009; Smith BJ 2011; Steinberg 2011) did not include a control group of usual care or less intensive counselling; the intervention tested in those studies was pharmacotherapy as an adjunct to behavioural support. Three studies that were performed in rehabilitation hospitals (Floter 2009; Haug 2011; Metz 2007) were also analysed separately from the studies conducted in acute care hospitals. Twenty-six studies (Bolman 2002; Borglykke 2008; Campbell 1991; Campbell 1996; CASIS 1992; Chouinard 2005; Cossette 2011; Croghan 2005; DeBusk 1994; Dornelas 2000; Feeney 2001; Froelicher 2004; Hajek 2002; Miller 1997; Mohiuddin 2007; Ortigosa 2000; Pedersen 2005; Pederson 1991; Pelletier 1998; Planer 2011; Quist-Paulsen 2003; Reid 2003; Reid 2007; Rigotti 1994; Rigotti 2006; Smith 2009; Taylor 1990) provided separate data by disease and contributed to the comparison of intervention versus control in different disease categories. We describe each intervention in Characteristics of included studies. We excluded 66 studies which appeared relevant but did not meet all inclusion criteria (see Characteristics of excluded studies). We did not include two studies (Brunner-Frandsen 2010; Jimenez 2007) for which there was insufficient data to make a decision, despite our efforts to contact the authors for additional information; these remain in the Characteristics of studies awaiting classification.
Advice to quit smoking and/or behavioural counselling was provided in all 50 studies. In 48 of them, a nurse or counsellor provided stop-smoking advice and/or behavioural counselling. Twelve studies included physician advice to quit (Campbell 1991; Campbell 1996; Croghan 2005; DeBusk 1994; Feeney 2001; Froelicher 2004; Hennrikus 2005; Lacasse 2008; Lewis 1998; Miller 1997; Ortigosa 2000; Pelletier 1998;), and in one study physician advice was offered prior to admission (Pederson 1991). In three studies, the patient chart was stamped with a prompt to remind the physician to offer smoking cessation advice (Rigotti 1997; Smith 2009; Smith PM 2011). Counselling ranged in duration from less than five minutes to two hours. In nine studies, counselling was delivered on more than one occasion during the hospitalisation period (Borglykke 2008; CASIS 1992; Cossette 2011; Floter 2009; Metz 2007; Nagle 2005; Ortega 2011; Pederson 1991; Rigotti 1994). Most studies also included materials such as self-help booklets, relaxation audio tapes and video tapes. In Haug 2011, participants were provided with access to an internet-based smoking cessation program and no face-to-face counselling was performed. In Smith BJ 2011, patients were referred to a quitline and were called by a quitline counsellor.
Forty-two of 50 studies (all except Bolman 2002; Croghan 2005; Hajek 2002; Hennrikus 2005; Molyneux 2003; Nagle 2005; Pederson 1991; Pelletier 1998) offered follow-up support following discharge. Of these, 29 offered support by telephone (Caruthers 2006; CASIS 1992; Chouinard 2005; Cossette 2011; de Azevedo 2010; DeBusk 1994; Dornelas 2000; Floter 2009; Froelicher 2004; Hasuo 2004; Hennrikus 2005; Lacasse 2008; Lewis 1998; Metz 2007; Miller 1997; Ortigosa 2000; Quist-Paulsen 2003; Rigotti 1994; Rigotti 1997; Rigotti 2006; Simon 1997; Simon 2003; Simon 2009; Smith 2009; Smith BJ 2011; Smith PM 2011; Stevens 1993; Stevens 2000; Taylor 1990), nine provided in-person support in various settings (Borglykke 2008; Campbell 1991; Campbell 1996; Meysman 2010; Mohiuddin 2007; Pedersen 2005; Reid 2003; Steinberg 2011; Vial 2002), and two offered support by telephone and/or in-person (Ortega 2011; Planer 2011). Two studies used newer technologies to contact patients after discharge: Haug 2011 provided individual feedback letters, an internet-based smoking cessation program and offered email support and Reid 2007 used an Interactive Voice Response (IVR) system. The duration of extended support ranged from one week to 12 months from discharge.
No studies tested the efficacy of pharmacotherapy with nicotine replacement therapy (NRT), bupropion, or varenicline versus placebo in the absence of a counselling intervention. However, six studies tested the marginal value of adding NRT to a counselling intervention (Campbell 1991; Campbell 1996; Lewis 1998; Molyneux 2003; Ortega 2011; Vial 2002), three studies tested the marginal value of adding bupropion to a counselling intervention (Planer 2011; Rigotti 2006; Simon 2009), and two trials tested the marginal value of adding varenicline to a counselling intervention (Smith BJ 2011; Steinberg 2011). One trial (Simon 2003) tested the marginal value of adding counselling to pharmacotherapy with NRT. In a number of other studies, particularly the newer ones, pharmacotherapy was allowed as part of the intervention or available to participants in the trial but was not specifically offered to all participants in one group and to none in another. Fourteen studies that reported providing NRT to a subgroup of patients did not specify the extent of its use (Borglykke 2008; Caruthers 2006; Chouinard 2005; DeBusk 1994; Froelicher 2004; Lacasse 2008; Pedersen 2005; Quist-Paulsen 2003; Reid 2003; Reid 2007; Rigotti 1997; Simon 1997; Simon 2003; Taylor 1990). Two studies included bupropion in a similar fashion (Chouinard 2005; Mohiuddin 2007) and in one study NRT, bupropion or varenicline were suggested during hospitalisation and follow-up (Cossette 2011).
Other study characteristics
Three studies compared two durations of post-discharge follow-up with a usual care control (Chouinard 2005; Hennrikus 2005; Miller 1997). Results from each arm of these studies were included separately in the analysis by intervention intensity. In four other studies that compared two intervention arms to a usual care control, the behavioural support offered in the two arms was comparable and results of the two intervention arms were combined in the analysis by intensity subgroups (Floter 2009; Lewis 1998; Molyneux 2003; Vial 2002). In Lewis 1998 and Molyneux 2003, the two intervention arms differed by the presence or absence of nicotine replacement, and these arms were directly compared in the pooled analysis of the effect of NRT. In Vial 2002, both intervention arms included the use of NRT, and compared follow-up from either a hospital or community pharmacist. In Floter 2009, both intervention arms included group counselling sessions during hospitalisation and follow-up with proactive telephone calls but the post-discharge intervention differed in style. In one study the smoking cessation intervention was part of a multicomponent risk intervention for patients with cardiovascular disease (DeBusk 1994); in this case the smoking cessation intervention was well-defined and met our inclusion criteria. Two studies had a third arm consisting of control patients who were not assigned randomly (de Azevedo 2010; Ortega 2011). We excluded the non-randomised patients from analyses of these studies.
Most studies (37 of 50) assessed cigarette abstinence 12 months after hospital discharge. Thirteen studies reported a shorter follow-up period of six months (Caruthers 2006; Cossette 2011; Croghan 2005; de Azevedo 2010; Floter 2009; Haug 2011; Lewis 1998; Meysman 2010; Pedersen 2005; Pederson 1991; Rigotti 1997; Simon 2009; Steinberg 2011). Fewer than half of the studies (20 of 50) used the preferred outcome measure, sustained abstinence. Twenty-eight studies used point prevalence abstinence as the outcome measure and two studies did not specify how abstinence was defined (Cossette 2011; Ortega 2011). One study reported sustained abstinence rates for overall cessation but point prevalence rates by diagnosis (Miller 1997).
All but two studies included both males and females; the exceptions (Floter 2009; Froelicher 2004) included only females. All studies included adults who smoked cigarettes currently or recently (e.g., within the past month). Seven studies included recent quitters as well as current smokers (CASIS 1992; DeBusk 1994; Haug 2011; Nagle 2005; Rigotti 1994; Stevens 1993; Stevens 2000).
Risk of bias in included studies
Fifteen of the fifty studies reported procedures for both random sequence generation and allocation concealment that we judged likely to avoid selection bias (Cossette 2011; de Azevedo 2010; DeBusk 1994; Froelicher 2004; Hajek 2002; Hasuo 2004; Lewis 1998; Nagle 2005; Reid 2003; Reid 2007; Rigotti 2006; Smith BJ 2011; Steinberg 2011; Taylor 1990; Vial 2002). Seventeen studies did not report the method of randomization and concealment in enough detail to judge the risk of selection bias, nine studies had low risk of selection bias for random sequence generation but unclear risk for allocation concealment, and three studies had unclear risk for random sequence generation and low risk for allocation concealment. Six studies did not allocate treatment at the individual patient level (Borglykke 2008; Bolman 2002; Haug 2011; Pelletier 1998; Stevens 1993; Stevens 2000). Two of them allocated treatment by alternating the intervention condition between hospitals over time (Stevens 1993, Stevens 2000) and one study employed a quasi-experimental design with one intervention and two control hospitals (Pelletier 1998). One study used a quasi-experimental design and assigned participants to intervention or control group according to bed availability in two wards of the same hospital (Borglykke 2008) while another used a quasi-randomized design where participants were assigned to control or intervention groups based on the calendar week of admission (Haug 2011). One other study (Bolman 2002) was not fully randomized; seven of 11 participating hospitals were randomized to condition, but four others selected their study arm. All six of these studies share the potential problems of recruitment bias and of underestimation of confidence limits due to intracluster correlation. Therefore, we conducted sensitivity analyses on the effect of excluding them.
The majority of studies (33 out of 50) reported numbers lost to follow-up and methods for addressing incomplete outcome data that we judged at low risk of attrition bias. Fourteen studies did not report enough information to be assessed for incomplete outcome data and were hence rated as unclear. Three studies were rated at high risk of attrition bias: Feeney 2001 assessed only those participants who attended a follow-up programme and hence had a large and unequal percentage of losses to follow-up; in Metz 2007, sensitivity analysis excluding losses to follow-up removes the significance of the study findings due to differential drop-out rates between study arms; and differential drop-out rates in Taylor 1990 increased the apparent effect of the intervention when using an intent-to-treat approach.
Most studies (41 of 50) used a method to validate subjects' self-reports of quitting at the follow-up assessment. Biochemical validation of smoking status was done in 32 studies, using expired air carbon monoxide in 15 studies (Campbell 1991; Campbell 1996; Caruthers 2006; CASIS 1992; Croghan 2005; DeBusk 1994; Hajek 2002; Lewis 1998; Mohiuddin 2007; Molyneux 2003; Ortigosa 2000; Reid 2003; Steinberg 2011; Taylor 1990; Vial 2002), and using plasma, salivary, or urinary cotinine in 17 studies (Chouinard 2005; DeBusk 1994; Feeney 2001; Froelicher 2004; Hajek 2002; Hasuo 2004; Hennrikus 2005; Lacasse 2008; Miller 1997; Nagle 2005; Quist-Paulsen 2003; Rigotti 1994; Rigotti 1997; Rigotti 2006; Simon 1997; Simon 2003; Simon 2009). Two studies used "corroboration by significant other" as the only validation method (Dornelas 2000; Smith 2009), and five other studies used "corroboration by significant other" in cases where a plasma or salivary cotinine measure was not available (Froelicher 2004; Lewis 1998; Miller 1997; Simon 2003; Smith 2009). Thirteen studies (Bolman 2002; Cossette 2011; de Azevedo 2010; Floter 2009; Haug 2011; Metz 2007; Meysman 2010; Pedersen 2005; Pelletier 1998; Planer 2011; Reid 2007; Stevens 1993; Stevens 2000) did not validate self-reported quitting at the follow-up assessment for any participants. Five others (Borglykke 2008; Ortega 2011; Pederson 1991; Reid 2003; Vial 2002) did not validate the smoking status of all participants who self-reported abstinence. Four studies used more than one means of validation other than corroboration by significant other (Chouinard 2005; DeBusk 1994; Rigotti 2006; Taylor 1990). In one study (Smith BJ 2011), validation of smoking abstinence with expired air carbon monoxide was performed only in a subsample but we used self-reported smoking abstinence rates in the analyses.
Most studies recruited participants on the basis of a convenience sample, with randomization being to group (intervention or control) rather than to initial inclusion. Participation rates (i.e., the proportion of those approached who agreed to take part in the trial) were also seldom recorded. Most studies recorded those lost to follow-up as continuing smokers. In one study (Stevens 2000), the intervention was offered inconsistently, with only 68% of those eligible for the intervention actually being approached.
Effects of interventions
Effect of counselling interventions categorised by intensity
|Figure 1. Forest plot of comparison: 1 Intervention v Control, by intensity of counselling intervention, outcome: 1.1 Quit at longest follow-up (6+ months).|
Only one included study (Hennrikus 2005) reported on the effect of a brief intervention in hospitalised patients with no follow-up after discharge (intensity 1). That study had a large sample size (>650 subjects per study arm). The brief intervention was no more effective than usual care (RR 1.14, 95% CI 0.82 to 1.59) although the confidence limits did not exclude the possibility of a benefit. Nine studies (Bolman 2002; Chouinard 2005; Croghan 2005; Hajek 2002; Meysman 2010; Molyneux 2003; Nagle 2005; Pederson 1991; Pelletier 1998) used a more intensive intervention in hospital but had no follow-up intervention component after discharge (intensity 2). There was no evidence of a significant benefit from pooling these studies and the confidence intervals suggest that any effect is likely to be small (RR 1.10, 95% CI 0.96 to 1.25, I² = 44%). Similar lack of statistically significant benefit was observed in a pooled analysis of the six studies that tested the effect of an intervention that began during hospitalisation and continued for up to 1 month after discharge (intensity 3). The risk ratio and confidence interval for the estimate of the effect of this level of intervention (RR 1.07, 95% CI 0.93 to 1.24, I² = 11%) is almost identical to that produced by the intensity 2 intervention.
In this update, we added eight new included studies that tested the highest intensity intervention (intensity 4), consisting of counselling that began in the hospital and continued for more than one month after discharge. The pooled estimate showed a statistically significant increase in quit rates that was similar to the previous review (RR 1.37, 95% CI 1.27 to 1.48, 25 studies) and heterogeneity remained relatively low (I² = 32%). This estimate excludes one study (Feeney 2001) which was an extreme outlier reporting a very large effect. In this trial amongst 198 patients admitted to a coronary care unit there was a very high drop out rate (79%) and low quit rate (1%) at 12 months in the usual care condition whilst the dropout rate was 55% and the quit rate 34% in the intervention group. The intervention group quit rate was comparable to that of other trials in the intensity 4 subgroup, but control group quit rates in the other trials were typically over 10%. This suggested that the difference in relative effect might have been due to characteristics of the support given to the control group and we decided to exclude this trial from the meta-analysis.
Three of the eight newly identified studies testing the most intensive intervention had a different design from the other trials (Caruthers 2006; Cossette 2011; Reid 2007). In these studies, all participants received the same intervention while in the hospital but were randomly assigned to interventions that differed after hospital discharge. We conducted a subgroup analysis limited to these trials in order to isolate the specific effect of a post-discharge intervention. The pooled estimate was a statistically significant 51% increase in smoking cessation rates (RR 1.51, 95% CI 1.03 to 2.22, I² = 44% Analysis 2.1) with the addition of a post-discharge counselling intervention.
The studies included in the preceding analyses were all conducted in acute care hospitals. We also identified three trials conducted in rehabilitation hospitals (Floter 2009; Haug 2011; Metz 2007), where patients are less acutely ill and length of stays are longer. Because of these differences, we chose to analyse studies from rehabilitation hospitals separately from studies in acute care hospitals. The interventions provided by studies based in the rehabilitation hospitals were of similar intensity; each provided over one month of follow-up contact after discharge (intensity 4), allowing us to pool the results. The pooled estimate was a statistically significant 71% increase in smoking cessation rates (RR 1.71, 95% CI 1.37 to 2.14, I² = 0% Analysis 3.1).
Some studies of behavioural counselling also included the option of pharmacotherapy, principally NRT. A sensitivity analysis excluding eighteen studies that reported the use of NRT within the highest intervention intensity did not suggest that the efficacy of these interventions was due to the use of NRT. The result from pooling only the seven trials that did not include the option of pharmacotherapy (CASIS 1992; de Azevedo 2010; Dornelas 2000; Hasuo 2004; Hennrikus 2005; Smith 2009; Smith PM 2011) though smaller, remained statistically significant (RR 1.24, 95% CI 1.09 to 1.41, I² = 0%).
Another sensitivity analysis excluded studies that did not randomly assign subjects to condition. Within studies that did not provide follow-up (intensity 2) we performed a sensitivity analysis excluding data reported by two studies that did not fully randomise patients (Bolman 2002; Pelletier 1998). The conclusion did not change (RR 1.03, 95% CI 0.87 to 1.22, I² = 44%). Within the group of studies that delivered an intervention with minimal follow-up (intensity 3) a sensitivity analysis excluding the data reported by two studies that did not randomise patients (Stevens 1993, Stevens 2000) slightly modified the point estimate, but did not substantially affect the confidence intervals (RR 1.01, 95% CI 0.83 to 1.21, I² = 0%). Within the group of studies with highest level of intensity of intervention (intensity 4), a sensitivity analysis excluding the data from one study that used a quasi-experimental design (Borglykke 2008) did not change the effect estimate (RR 1.35, 95% CI 1.25 to 1.46, I²= 28%).
Approximately half of the studies that delivered the highest intervention intensity (intensity 4) excluded smokers who were not willing to attempt cessation after discharge. We performed a sensitivity analysis excluding the data reported by 13 studies in which participants were selected on the basis of their willingness to make a quit attempt (Caruthers 2006; Cossette 2011; DeBusk 1994; Froelicher 2004; Hasuo 2004; Lacasse 2008; Lewis 1998; Miller 1997; Reid 2003; Simon 1997; Smith PM 2011; Taylor 1990; Vial 2002). An intervention effect persisted in the remaining 12 studies (RR 1.44, 95% CI 1.28 to 1.62, I² = 43%).
We performed a sensitivity analysis excluding studies that enrolled former smokers (defined as having not smoked for more than one month before admission) as well as current smokers (CASIS 1992; DeBusk 1994; Nagle 2005; Rigotti 1994; Stevens 1993; Stevens 2000, Taylor 1990;). For intensity 3 (studies delivering a minimal intensity intervention with short-term follow-up), limiting the analysis to current smokers produced little change in the result (RR 1.01, 95% CI 0.82 to 1.24, I² = 0%). For studies delivering the highest intervention intensity (intensity 4), a statistically significant increase in quitting remained even after the exclusion of studies that included quitters, and the point estimate changed little (RR 1.35, 95% CI 1.24 to 1.48, I² = 35%). In the update, only one new study included both current smokers and recent former smokers who had quit for six months or less (Haug 2011), and this study was performed in a rehabilitation setting. Excluding this study from the analysis did not significantly change the estimate but only two studies remained in the analysis for rehabilitation centres (RR 1.56, 95% CI 1.20 to 2.03, I² = 0%).
We performed a sensitivity analysis excluding 15 studies that did not validate self-reported smoking cessation outcomes (Bolman 2002; Borglykke 2008; Cossette 2011; de Azevedo 2010; Floter 2009; Haug 2011; Metz 2007; Meysman 2010; Pedersen 2005; Pelletier 1998; Planer 2011; Reid 2007; Smith BJ 2011; Stevens 1993; Stevens 2000). This did not alter the results. The point estimates for the lower intensity interventions declined, but confidence intervals remained wide and conclusions did not change (intensity 2 RR 0.96, 95% CI 0.81 to 1.14, I² = 0%; intensity 3 RR 1.01, 95% CI 0.83 to 1.21, I² = 0%). Five studies in the most intensive intervention category (intensity 4) did not validate self-reported smoking cessation (Borglykke 2008; Cossette 2011; de Azevedo 2010; Pedersen 2005; Reid 2007). Excluding them did not alter the point estimate or statistical significance of the effect (RR 1.38, 95% CI 1.28 to 1.50, I² = 32%).
Effect of pharmacotherapy
The effect of pharmacotherapy compared with placebo as a single intervention in the absence of counselling has not been tested. Several trials have tested the effect of adding pharmacotherapy to a counselling intervention or, conversely, of adding counselling to a pharmacotherapy intervention.
Six trials (Campbell 1991, Campbell 1996, Lewis 1998; Molyneux 2003; Ortega 2011; Vial 2002) tested the marginal effect of NRT added to counselling. In these trials, NRT was compared with placebo NRT or no NRT and all subjects received a counselling intervention. Pooled analysis of these studies produced a significant RR of 1.54 (95% CI 1.34 to 1.79, I² = 33%, Analysis 4.1.1). This result is consistent with the effect of NRT seen in other settings (Stead 2008b). One trial compared the effect of adding intensive counselling versus minimal counselling to an NRT intervention (Simon 2003). The study had an RR of 1.68 for sustained abstinence, but the confidence limits of that estimate missed statistical significance (95% CI 0.80, 3.53). However, the result was consistent with the impact of intensive counselling observed in the absence of pharmacotherapy.
Three studies systematically compared the use of bupropion with placebo among hospitalised smokers who also received intensive smoking cessation counselling (Planer 2011; Rigotti 2006; Simon 2009). The pooled analysis did not detect a statistically significant effect of the drug over intensive counselling alone (RR 1.04, 95% CI 0.75 to 1.45, I² = 29%, Analysis 4.1.2). While the confidence limits were wide, they do not encompass the confidence limits for the effect of bupropion in other settings (OR 1.94, 95% CI 1.72 to 2.19, Hughes 2007), suggesting that bupropion may not be effective, or may be less effective, when started in the hospital.
Two studies of varenicline compared the use of varenicline with placebo (Steinberg 2011) or counselling alone (Smith BJ 2011). The pooled estimate suggested an effect of the drug over intensive counselling alone (RR 1.29, 95% CI 0.95 to 1.76) but the wide confidence limits reflect the small numbers of participants (580) and the result was not statistically significant. There was also heterogeneity between the two studies (I²= 62%), with Steinberg 2011 reporting lower quit rates in the varenicline group.
Effect of intervention by diagnosis
The included studies were heterogeneous in the types of hospitalised patients who were recruited. Because of this diagnostic heterogeneity, we examined the results of interventions within the following diagnostic groups, keeping the same intensity subgroups where the number of studies justified this approach. Seventeen studies enrolled hospital patients with a wide range of admitting diagnoses. These studies tested smoking intervention programs that were implemented hospital-wide (Caruthers 2006; de Azevedo 2010; Hasuo 2004; Hennrikus 2005; Lewis 1998; Miller 1997; Molyneux 2003; Nagle 2005; Rigotti 1997; Simon 2003; Simon 2009; Smith BJ 2011; Smith PM 2011; Steinberg 2011; Stevens 1993; Stevens 2000; Vial 2002). Twenty-two studies reported on the effects of interventions in patients hospitalised with a cardiovascular diagnosis (Bolman 2002; Campbell 1991; CASIS 1992; Chouinard 2005; Cossette 2011; DeBusk 1994; Dornelas 2000; Froelicher 2004; Hajek 2002; Miller 1997; Mohiuddin 2007; Ortigosa 2000; Pedersen 2005; Pelletier 1998; Planer 2011; Quist-Paulsen 2003; Reid 2003; Reid 2007; Rigotti 1994; Rigotti 2006; Simon 2009; Taylor 1990). Five studies reported on interventions in patients with a respiratory diagnosis (Borglykke 2008; Campbell 1991;Campbell 1996; Miller 1997; Pederson 1991). Only one small pilot study was found that recruited hospitalised patients admitted for a cancer diagnosis (Croghan 2005).
The pattern of effect across intervention intensities was similar for the eighteen studies that enrolled patients with all admitting diagnoses ( Analysis 5.1). Interventions categorized as intensity 4 were effective in a pooled analysis of twelve studies in this subgroup (RR 1.26, 95% CI 1.12 to 1.42, I² = 25%). The risk ratio was lower than the effect of the intensity 4 intervention in the overall analysis, but the confidence intervals overlap and we cannot conclude that intensive interventions are less effective in this subgroup. Pooled analysis of less intensive interventions demonstrated no effect and did not differ from the overall analysis (intensity 2: RR 0.90, 95% CI 0.64 to 1.28, I² = 0%, 2 studies; intensity 3, RR 1.10, 95% CI 0.94 to 1.29, I² = 28%, 4 studies).
The estimate of the effect for each level of intervention intensity among patients with a cardiovascular diagnosis was also very similar to that for the entire sample of hospitalised patients ( Analysis 5.2). Pooled analysis of 14 studies reporting on the effect of the most intensive intervention (intensity 4) found a statistically significant effect (RR 1.42, 95% CI 1.29 to 1.56, I² = 32%, CASIS 1992; Chouinard 2005; Cossette 2011; DeBusk 1994; Dornelas 2000; Froelicher 2004; Miller 1997; Mohiuddin 2007; Pedersen 2005; Quist-Paulsen 2003; Reid 2003; Reid 2007; Smith 2009; Taylor 1990). The point estimate of the effect was similar to that for overall analysis (RR 1.37, 95% CI 1.27 to 1.48), the confidence intervals overlap substantially, and we cannot conclude that interventions in patients hospitalised for cardiovascular disease are more effective than in the general hospital population. No statistically significant effect was found for interventions of lower intensity. Pooled analysis of four studies of in-hospital counselling without follow-up after discharge (intensity 2) found no intervention effect (RR 1.10, 95% CI 0.94 to 1.28, I² = 58%, Bolman 2002; Chouinard 2005; Hajek 2002; Pelletier 1998). Pooled analysis of three studies that provided in-hospital counselling and brief follow-up contact after discharge (intensity 3) also found no intervention effect (RR 1.04, 95% CI 0.84 to 1.28, I² = 0%, Miller 1997; Ortigosa 2000; Rigotti 1994).
One of the trials that tested an intensity 4 smoking intervention in the cardiovascular subgroup (Mohiuddin 2007) also assessed all-cause mortality and hospital readmission rates as endpoints. Over a two-year follow-up, the intervention produced a relative risk reduction of 0.77 (95% CI 0.27 to 0.93, p=.014) in all-cause mortality and a relative risk reduction of 0.44 (95% CI 0.16 to 0.63, p=.007) in hospital readmissions.
Five studies provided interventions to patients hospitalised with a respiratory diagnosis. Two of these studies evaluated NRT (Campbell 1991; Campbell 1996) and three other studies of counselling interventions used different intensity interventions (Borglykke 2008; Miller 1997; Pederson 1991). We estimated a separate pooled effect for the NRT studies (RR 1.29, 95% CI 0.62 to 2.69, I² = 65%) and for the counselling studies (RR 1.22, 95% CI 0.93 to 1.60, I² = 76%).
One pilot study reported on the effects of a hospital-based intervention for patients with cancer (Croghan 2005). It found no evidence of efficacy but the sample size was very small and the confidence limits were very broad.
The results of this review indicate that smoking cessation counselling interventions delivered during a period of hospitalisation and including follow-up support that lasts at least one month after discharge increase smoking cessation rates. The estimated effect of such interventions was to increase the smoking cessation rate by 37% at six to 12 months after hospital discharge. This finding was robust. It remained statistically significant in sensitivity analyses that excluded studies of lower quality (e.g., those that did not validate self-reported smoking cessation at outcome or those that were not randomized). Neither the exclusion of studies that included recent quitters as well as current smokers nor those that included patients selected for motivation significantly affected the relative effect of intervention over control. This review found no evidence to of an effect of less intensive counselling interventions, such as those delivered only during hospitalisation or those which include less than one month of follow-up support after discharge. Therefore, post-discharge follow-up support appears to be an important component of interventions that begin during hospitalisation. We caution that the effect sizes observed in all these studies may be artificially modest because in many cases the "control" condition was more intensive than usual care or simply brief advice.
The counselling intervention in these studies was generally delivered by a research nurse or trained smoking cessation counsellor, not by a nurse responsible for other aspects of the patients' clinical care. Physician advice was a component of the intervention in many trials. There is no specific evidence from this review that brief physician advice to quit is effective by itself in the hospital setting, although evidence from trials in primary care settings support the efficacy of physician advice to quit (Stead 2008a). Pharmacotherapy with nicotine replacement therapy (NRT), bupropion, or varenicline was included in some of the counselling studies, especially the more recent ones. In most of these trials, the pharmacotherapy was not systematically provided to all subjects in the intervention arm or excluded from all subjects in the control arm. The efficacy of counselling interventions remained after excluding those studies that reported the use of NRT, suggesting that counselling alone is effective.
This update includes a new finding regarding pharmacotherapy. In hospitalised smokers the effect of pharmacotherapy by itself, compared to placebo or no pharmacotherapy in the absence of counselling, cannot be determined because no such trials have been conducted. However, the marginal effect of NRT, bupropion, or varenicline when added to counselling in the hospital setting has been tested. Pooled analysis of six studies found a statistically significant 54% increase in the smoking cessation rate when NRT was added to counselling alone. This finding is new since the 2007 update, at which time there was a non-significant trend toward finding the addition of NRT to counselling to be efficacious in the hospital setting. The current estimate of the effect of NRT in the hospital setting is within the confidence intervals of the estimated RRs from the Cochrane review of NRT: 1.43 (95% CI 1.33 to 1.53) for nicotine gum and 1.66 (95% CI 1.53 to 1.81) for nicotine patch (Stead 2008b). Hence these data support NRT's usefulness in appropriate patients during and following hospitalisation. Starting NRT before discharge was associated with a higher rate of NRT use two weeks after discharge in a non-randomized observational trial in one hospital (Regan 2011). The marginal effect of counselling when added to NRT begun in the hospital was tested in only one study (Simon 2003). Intensive counselling increased the rate of smoking cessation over that achieved by NRT alone, but the result was not statistically significant (RR 1.68,95% CI 0.80, 3.53). However, the result was consistent with the pooled estimate from this review of the effect of intensive counselling without pharmacotherapy.
Fewer data are available to assess the benefit of bupropion or varenicline as adjuncts to smoking cessation counselling that starts in the hospital setting. This update identified two new trials of bupropion to add to one previous trial (Rigotti 2006). All three trials tested the marginal efficacy of bupropion over placebo among smokers who all received intensive counselling in the hospital setting. Bupropion was not more effective than placebo in the pooled analysis (RR 1.06, 95% CI 0.68 to 1.63). This finding contrasts with evidence that bupropion is effective for smoking cessation in other populations (Hughes 2007). A possible explanation for the lack of efficacy of bupropion in the context of hospitalisation is the long half-life of sustained-release bupropion. Steady-state bupropion blood levels occur only after five to seven days of drug administration. This is generally after hospital discharge. Consequently, hospitalised smokers may be discharged into an environment filled with cues to smoke before they have sufficient levels of bupropion for it to be effective.
This update also identified the first randomized controlled trials that tested the efficacy of initiating varenicline in the hospital setting. Two trials compared the efficacy of adding varenicline (versus placebo or no drug) to counselling in the hospital setting. The pooled result of these studies produced an estimated 28% increase in the rate of smoking cessation with varenicline, but the result was not statistically significant and confidence intervals were wide due to the small sample sizes of the trials (95% CI 0.88 to 2.26). This contrasts with strong evidence of efficacy and a higher estimate of the effect size of varenicline that has been found in a systematic review of varenicline (RR 2.27, 95% CI 2.02 to 2.55, Cahill 2012).
The analyses by diagnosis demonstrate that the intensive counselling intervention was independent of the patient's admitting diagnosis . The absolute cessation rates amongst smokers admitted with cardiovascular disease tended to be higher than amongst smokers not selected by diagnosis, but the relative effect of an intensive counselling intervention was not significantly greater in CVD patients. The potential benefit of intensive intervention in smokers with CVD was illustrated in the one study that assessed health care utilization and mortality outcomes (Mohiuddin 2007). That study found a large increase in smoking cessation in the intervention group, and at two-year follow-up, a substantial decline in hospital readmission and all-cause mortality rates. There was a possibility of confounding due to better control of blood pressure and cholesterol and better medication compliance in the intervention group. Among smokers hospitalised for myocardial infarction, intensive counselling begun in the hospital is highly cost effective, even when the cost of a course of pharmacotherapy is included in the calculation (Ladapo 2011). The effectiveness of smoking cessation interventions for patients who are admitted to hospital with a respiratory diagnosis is less clear, in part because of a small number of studies in this subgroup. Overall, there is no strong evidence for a differential effect of the intensive counselling intervention by diagnosis. These data support offering hospital-based interventions to all smokers, regardless of admitting diagnosis.
Determining how to translate these findings effectively and consistently into routine clinical practice is the next challenge for this field. The intervention in most of the trials included in this review was delivered by research staff. The effectiveness of implementing the intervention in routine clinical practice, where interventions will be delivered by clinical staff, needs to be demonstrated. Feasible models that can be readily implemented in hospital settings are needed. Current evidence on this point is limited. Two studies included in this review illustrate this challenge (Stevens 1993; Stevens 2000). Both studies provided a similar counselling intervention in a similar setting, but counselling was delivered by research staff (masters-level psychologists) in the first study and by clinical staff (trained respiratory therapists) in the second study. The intervention efficacy was demonstrated in the first study but did not persist in the second study. The feasibility of maintaining an efficacious intervention after the conclusion of a research trial was investigated for another study included in this systematic review (Miller 1997). The counselling intervention was maintained in the same hospitals for three years after the clinical trial ended. During that time approximately half of the smokers accepted the offer of intervention, and those smokers had a cessation rate comparable to that achieved in the randomized trial. These results suggested that programme effectiveness was maintained (Smith 2002). More studies are needed to demonstrate the feasibility and effectiveness of hospital-initiated smoking cessation interventions in routine practice.
Finally, this update includes the first studies conducted in rehabilitation hospitals. The results of the pooled analysis finds that smoking interventions in these settings are effective and extend the effect from acute care hospitals to a broader group of settings.
Implications for practice
The results support the use of smoking cessation counselling interventions that begin during the hospitalisation period and include at least one month of follow-up supportive contact after discharge. There is no evidence of an effect of less intensive counselling interventions, particularly those that do not continue after hospital discharge, on smoking cessation. The effect of the counselling intervention does not clearly vary by a smoker's admitting diagnosis, and it is appropriate to offer the intervention to hospitalised smokers regardless of their admitting diagnosis. Adding nicotine replacement therapy to an intensive counselling intervention further increases the effect of hospital-initiated interventions and should be routinely offered. There is insufficient evidence regarding the benefit of adding varenicline or bupropion to counselling, although there was a trend toward statistical significance for varenicline and the results are compatible with data which show the efficacy of varenicline in other settings. Bupropion may not have an effect when added to counselling started in the hospital.
Implications for research
The impact of an intensive counselling intervention that continues after hospital discharge is well-established. The effect of adding NRT to a counselling intervention in hospitalised patients is now also established, with a relative risk estimate that is consistent with the established efficacy of NRT. Further studies testing the efficacy of adding varenicline to counselling are warranted in view of the results of early studies. They might generate sufficient data to produce a statistically significant result in future pooled analyses. The pooled evidence of studies with bupropion does not provide support for further studies of the drug in this context.
Research is needed to identify effective strategies for implementing and disseminating this evidence into routine practice in health care systems.
Additional research is needed to assess the cost-effectiveness of the intensive counselling intervention and to explore the impact of counselling on health and healthcare utilization outcomes.
Mike Murphy was an author on the original version of this review (2001, Issue 2), and on the first update (2003, Issue 1). The authors would like to thank Sarah Welch and Sarah Roberts of the ICRF General Practice Research Group for their assistance in extracting data for the original review, Nete Villebro, Hitomi Kobayashi and Roland Fischer for their assistance in translating and extracting data, and Corinne Husten, John Britton and Ian Campbell for helpful comments during peer review. Jamie Hartmann-Boyce completed the expanded Risk of Bias tables for studies included in the review prior to the 2012 update.
Data and analyses
- Top of page
- Authors' conclusions
- Data and analyses
- What's new
- Contributions of authors
- Declarations of interest
- Sources of support
- Index terms
Appendix 1. Details of search strategies for Tobacco Addiction register and CINAHL
Search strategy for the Tobacco Addiction specialised register:
(hospital and patient*) or hospitali* or inpatient* or admission* or admitted
Search strategy for CINAHL (EBSCO):
S14 S4 and S5 and S13
S13 S6 or S7 or S8 or S9 or S10 or S11 or S12
S12 MH Placebos
S11 TX RCT
S10 MH (Random assignment OR Clinical Trials+ OR Quantitative Studies)
S9 TX "control group*"
S8 TX "treatment arm"
S7 TX (trial and (control* OR comparative))
S6 TX (random* OR factorial* OR placebo* OR assign* OR allocat*
S5 MJ (smok* OR tobacco OR nicotine)
S4 S1 or S2 or S3
S3 MJ (hospitali* OR inpatient*)
S2 TI (hospitali* OR inpatient* OR admission* OR admitted) or AB (hospitali* OR inpatient* OR admission* OR admitted)
S1 TI (hospital with patient*) or AB (hospital with patient*)
Appendix 2. Glossary of tobacco-specific terms
Last assessed as up-to-date: 8 March 2012.
Protocol first published: Issue 4, 1999
Review first published: Issue 2, 2001
Contributions of authors
NR and CC extracted data for the 2012 update, with input from LS. NR and CC wrote the update, with input from MM and LS. All authors except CC were involved in the conception, data extraction and writing of the original review.
Declarations of interest
Dr Rigotti was the co-author of three studies included in the review. Dr. Rigotti's research is funded by the U.S. National Institutes of Health, by private nonprofit foundations, and by the pharmaceutical companies that make investigational or approved smoking cessation products. Her work on this review was funded by a Midcareer Investigator Award in Patient-Oriented Research from the U.S. National Heart Lung and Blood Institute. Marcus Munafò has received grant funding from Pfizer through their Investigator Initiated Research programme.
Sources of support
- Department of Primary Health Care, Oxford University, UK.
- NHS Research and Development Programme, UK.
- NIH / NHLBI Mid-career Investigator Award in Patient Oriented Research (#K24-044440), USA.
Medical Subject Headings (MeSH)
*Inpatients; *Smoking Cessation; Counseling [methods]; Hospitalization; Patient Education as Topic [*methods]; Randomized Controlled Trials as Topic; Sensitivity and Specificity; Smoking [*prevention & control]
MeSH check words
* Indicates the major publication for the study