Interventions for smoking cessation in people undergoing lung cancer screening.

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Learn more: PMC Disclaimer | PMC Copyright Notice Cochrane Database Syst Rev . 2026 May 29;2026(5):CD016184. doi: 10.1002/14651858.CD016184 Interventions for smoking cessation in people undergoing lung cancer screening Henry M Marshall 1, 2, 3, 4 , Hollie Bendotti 2, 5 , Kylie Morphett 5, 3 , Nathan J Harrison 6, 3, 7 , Jana Y Waldmann 8, 9 , Gary Chan 3, 10 , Anne Fidler 11 , Stacey Allerton 11 , Catherine Runge 12 , Mark Brooke 12 , Sheleigh Lawler 5, 3 , Coral E Gartner 5, 3 , Ian A Yang 1, 2, 4 , Kwun Fong 1, 2, 4 Editor: Cochrane Central Editorial Service Author information Article notes Copyright and License information 1 Department of Thoracic Medicine, The Prince Charles Hospital, Brisbane, Australia 2 UQ Thoracic Research Centre, Faculty of Health, Medicine and Behavioural Science, The University of Queensland, Brisbane, Australia 3 NHMRC Centre of Research Excellence on Achieving the Tobacco Endgame, School of Public Health, The University of Queensland, Brisbane, Australia 4 NHMRC Centre of Research Excellence to Prevent and Detect Curable Lung Cancer, The University of Queensland, Brisbane, Australia 5 School of Public Health, Faculty of Health, Medicine and Behavioural Science, The University of Queensland, Brisbane, Australia 6 Flinders Health and Medical Research Institute, College of Medicine and Public Health, Flinders University, Adelaide, Australia 7 National Centre for Education and Training on Addiction, Flinders Health and Medical Research Institute, College of Medicine and Public Health, Flinders University, Adelaide, Australia 8 Library Services, The Prince Charles Hospital, Brisbane, Australia 9 Faculty of Health, Medicine and Behavioural Science, The University of Queensland, Brisbane, Australia 10 National Centre for Youth Substance Use Research, University of Queensland, Brisbane, Australia 11 White Daisy Project Australia - Lung Cancer Awareness, Brisbane, Australia 12 Lung Foundation Australia, Brisbane, Australia ✉ Henry M Marshall, The Department of Thoracic Medicine, The Prince Charles Hospital, Rode Road, Chermside, Brisbane, Queensland, 4032, Australia. henry.marshall@health.qld.gov.au . Collection date 2026. Copyright © 2026 The Authors. Cochrane Database of Systematic Reviews published by John Wiley & Sons, Ltd. on behalf of The Cochrane Collaboration. This is an open access article under the terms of the Creative Commons Attribution-Non-Commercial Licence , which permits use, distribution and reproduction in any medium, provided the original work is properly cited and is not used for commercial purposes. The content of this article (as distinct from the content of the ‘Supplementary materials’, ‘Related’ and ‘About this Review’ sections) has been peer reviewed and prepared for publication in accordance with Cochrane’s editorial policies . Though the aim of these processes is, among other things, to check the accuracy of such content, responsibility for the content remains that of the author(s) and Cochrane gives no representations or warranties of any kind in relation to, and accepts no liability for any reliance on or use of, the content of the article. PMC Copyright notice PMCID: PMC13220720  PMID: 42212788 Objectives This is a protocol for a Cochrane Review (intervention). The objectives are as follows: To assess the benefits and harms of smoking cessation interventions in adults undergoing lung cancer screening with low‐dose computed tomography (LDCT) of the chest. Background Description of the condition Lung cancer is the world‐leading cause of cancer mortality, responsible for 1.8 million deaths in 2022 [ 1 ]. At present, most people with lung cancer are diagnosed at an advanced stage of disease, meaning cure is less likely. Lung cancer screening (LCS) aims to reverse this clinical paradigm by detecting lung cancer at an early stage, when cure is most likely. LCS using low‐dose computed tomography (LDCT) results in a 21% mortality reduction [ 2 ]. Surgical resection of screen‐detected early‐stage lung cancer leads to a 10‐year lung cancer‐specific survival rate of 73.9% to 95% [ 3 , 4 ], compared with the current five‐year survival of around 10% to 20% in most world regions [ 5 ]. Tobacco smoke is the main cause of lung cancer. Smoking is closely linked to sociodemographic variables. Smoking prevalence is much higher in certain populations, including rural and remote dwellers; lesbian, gay, bisexual, transgender, intersex, queer, and other sexuality and gender diverse (LGBTIQ+) people; people living with mental illness; people living with disabilities; and Indigenous peoples [ 6 , 7 , 8 , 9 ]. Smoking is strongly linked to socioeconomic disadvantage and drives health and social inequity, which is transmitted across generations [ 10 ]. Because of its close link to smoking, lung cancer is more common in populations with higher smoking prevalence and thus both arises from and contributes to health inequity [ 11 ]. Primary prevention of tobacco‐related lung cancer involves reducing smoking exposure by decreasing smoking uptake and supporting smoking cessation and abstinence. Combining primary prevention with early detection through LCS could yield better lung cancer outcomes than either strategy used alone [ 12 ]. In addition, even if lung cancer is diagnosed, smoking cessation improves prognosis, survival, and clinical outcomes at every disease stage [ 13 ]. Description of the intervention and how it might work Smoking cessation interventions employ a range of behavioural and pharmacological components, which are often used in combination. Interventions range from very brief advice, which can be provided within a few minutes, through to multisession counselling supported by weeks to months of pharmacotherapy. More recently, digital interventions such as smartphone apps have become available to help people quit. Pharmacological treatments aim to reduce cravings and withdrawal symptoms whilst the person reduces or stops their cigarette consumption; they also attenuate the rewarding effects of smoking itself. This allows time for the person to develop and practise behavioural strategies to deal with the habitual, social, and emotional components of nicotine addiction. Screening programmes offer many opportunities to engage the eligible population for smoking behaviour change, and smoking cessation interventions are considered an essential component of LCS programmes [ 14 , 15 ]. Multiple studies report higher quit rates in LCS participants than the general population, especially if the scan shows abnormal findings [ 16 , 17 ]. However, it is unclear which models of care deliver the best smoking cessation outcomes in LCS. Extrapolating smoking cessation trial findings from general populations to screening populations may not be valid, because LCS populations are often older and more likely to have medical comorbidities, long‐standing smoking exposure, and multiple prior quit attempts, highlighting the complexity of behavioural change in this population [ 18 ]. One systematic review including 10 randomised controlled trials (RCTs) found that smoking cessation interventions delivered during LCS doubled quit rates compared to usual care (odds ratio (OR) 2.01; 9 RCTs), and more intensive interventions had a greater effect than less intensive interventions (OR 2.07; 2 RCTs) [ 19 ]. Although less intensive interventions (e.g. providing brochures or brief advice) appear less effective than more intensive interventions (e.g. multiple counselling sessions with or without pharmacological therapy), there is insufficient evidence to support a particular approach [ 20 ]. Even mildly effective interventions at the individual level may greatly enhance screening programme impact at the broader population level. For example, an intervention with 10% quit success would further reduce lung cancer deaths by 14% and increase life‐years gained by 81% compared with screening alone [ 21 ]. Why it is important to do this review Establishing the evidence for best practice smoking cessation interventions in LCS is a priority identified by many professional bodies and societies, including the European Respiratory Society, the National Institutes of Health (NIH), the US National Academy of Science, the Society for Research on Nicotine and Tobacco, and the American Thoracic Society [ 20 , 22 , 23 ]. Smoking is the leading behavioural cause of preventable death and disability worldwide. Providing comprehensive cessation support is a key World Health Organization (WHO) measure in reducing the demand for, and prevalence of, tobacco use [ 24 ]. Because smoking has been and remains highly prevalent, a very large population is at risk of lung cancer and eligible for screening. In the USA, nearly 13 million people are eligible for LCS [ 25 ]. Between half and three‐quarters of people undertaking LCS currently smoke, amounting to millions of people worldwide who would benefit from smoking cessation interventions in combination with LCS. Targeted LCS programmes are gaining momentum in many countries, following implementation in the USA in 2013. For example, England and Australia announced funding for national LCS programmes in 2023 [ 26 , 27 ]. Quitting smoking reduces all‐cause and lung cancer‐specific mortality and improves LCS cost‐effectiveness. A post‐hoc analysis of data from the National Lung Screening Trial (NLST; the largest RCT of lung cancer screening in the world) showed that quitting for seven years conferred the same 21% mortality reduction as LDCT screening for three years [ 12 ]. Long‐term smoking abstinence (15 years) reduced lung cancer‐specific mortality by 38% when combined with LCS. Multiple modelling studies of smoking cessation and LCS have reported similar benefits [ 28 , 29 , 30 , 31 , 32 , 33 , 34 , 35 , 36 , 37 , 38 , 39 , 40 , 41 , 42 ]. Beyond lung cancer‐specific outcomes, 15 years' smoking abstinence reduces excess cardiovascular risk to that of a person who has never smoked [ 43 ], pointing to all‐cause mortality benefits beyond lung cancer. Improving smoking cessation amongst people undergoing LCS can therefore have significant individual and programme/population health and cost‐effectiveness benefits. This systematic review and meta‐analysis represents an important opportunity to synthesise evidence to inform implementation of best practice smoking cessation interventions for people undergoing LCS around the world. Objectives To assess the benefits and harms of smoking cessation interventions in adults undergoing lung cancer screening with low‐dose computed tomography (LDCT) of the chest. Methods We will follow the Methodological Expectations of Cochrane Intervention Reviews (MECIR) when conducting the review [ 44 ], and PRISMA 2020 for the reporting [ 45 ]. Criteria for considering studies for this review Types of studies We will include RCTs with individual or cluster randomisation. Quasi‐randomised studies will be ineligible. We will include data from all types of publications, as well as unpublished data where available. There will be no language restrictions. For reports published in a language that no review authors understand, we will use Google Translate to determine whether the study meets our eligibility criteria. If we include any such studies, we will attempt to find a native language speaker to help with translation and data extraction (e.g. via Cochrane Engage); if this is not possible, we will use Google Translate. Types of participants We will include trials of asymptomatic adults who smoke and who are participating in, or eligible for, LDCT lung cancer screening, regardless of motivation to quit. Individuals with symptoms suggestive of lung cancer are not eligible for LCS. Eligibility for LCS may vary slightly between studies, but generally these programmes include older people (e.g. aged > 50 years) with more extensive smoking histories (e.g. ≥ 20 pack‐years, where 1 pack‐year = 20 cigarettes/day for 1 year) [ 2 ]. Some LCS programmes use multivariable risk prediction models to determine eligibility, but this method still selects older and more tobacco‐exposed individuals. Health inequalities are unfair and avoidable differences across socially stratifying factors that limit opportunities for health. Smoking is strongly linked to socioeconomic disadvantage and health inequity. We will assess potential disadvantage through the components of the PROGRESS‐Plus acronym (Place of residence, Race/ethnicity/culture/language, Occupation, Gender or sex, Religion, Education, Socioeconomic status, Social capital, age, sexual orientation, and disability) [ 46 ]. We do not plan to conduct a formal equity analysis, but will discuss the PROGRESS‐Plus data in the 'Discussion' section. Types of interventions We will include all types of behavioural and pharmacological interventions to assist smoking abstinence. Behavioural interventions may include, but are not limited to, counselling by telephone/telehealth or face‐to‐face, as a group or individual; brief interventions delivered in single or multiple sessions; and printed or digital resources, including internet‐, text message‐, or smartphone‐based resources. We will categorise behavioural intervention components as described in the Cochrane overview of behavioural interventions for smoking cessation, according to the following factors [ 47 ]. Behavioural components (e.g. counselling, biofeedback, financial incentives). Delivery mode (e.g. group, individual, face‐to‐face, telephone). Intervention provider (e.g. nurse, psychologist/counsellor). Intensity of the intervention (e.g. duration, frequency, count). Pharmacological interventions may include, but are not limited to, nicotine replacement therapy, bupropion, varenicline, nortriptyline, and cytisine. Electronic cigarettes may also be included. We will include trials comparing different regimens of an intervention (e.g. frequency, dose, duration), comparing multiple interventions to a single type, and combinations of these. Interventions may be delivered by any health staff (e.g. doctor, nurse, psychologist, counsellor). The intervention may be started before, at the time of, or after the LDCT scan. Comparison groups must include one of the following. Placebo. No treatment. Another smoking cessation intervention. For our critical outcome of smoking abstinence at six months and important outcome of adverse/serious adverse events at six months, we will focus on the following comparisons. Pharmacotherapy plus behavioural therapy versus control. Pharmacotherapy versus control. Behavioural therapy versus control. Outcome measures If eligible studies report none of our critical or important outcome measures, we will check preregistered protocols for outcomes that were unreported in included sources, and we will contact the study authors to ascertain availability of outcome data for inclusion in the meta‐analysis. Critical outcomes Smoking abstinence at six months' follow‐up or longer. We will include all definitions of smoking abstinence but will select the strictest definition if study authors use more than one (sustained, prolonged, or continuous abstinence in preference to point prevalence; biochemically validated abstinence in preference to self‐reported abstinence; and biochemically validated point prevalence abstinence in preference to self‐reported continuous or prolonged abstinence). Serious adverse events (resulting in death, a life‐threatening condition, hospitalisation, or persistent significant disability) assessed as the number of participants with at least one event at six months Important outcomes Biochemically validated or self‐reported smoking abstinence at less than six months but more than four weeks of follow‐up Reductions in smoking behaviour, measured in cigarettes per day, from baseline to follow‐up assessment Participant quit attempts, defined as smoking abstinence greater than 24 hours Adverse events, assessed as the number of participants with at least one event at six months Search methods for identification of studies Electronic searches We prepared a draft search strategy in collaboration with an Information Specialist (JW). Supplementary material 1 presents the search strategies for CENTRAL, MEDLINE, and Embase. An independent information specialist reviewed the search strategy for MEDLINE using the Peer Review of Electronic Search Strategies (PRESS) tool [ 48 ]. We will limit the search to studies published from 1996 (when the first cohort study of LDCT lung cancer screening was published). We will search the following electronic databases. Cochrane Lung Cancer Group Trial Register. Cochrane Tobacco Addiction Review Group Specialised Register. Cochrane Central Register of Controlled Trials (CENTRAL; Wiley; 1996 to present). MEDLINE (Ovid; 1996 to present). Embase (Elsevier, Embase.com; 1996 to present). PsycINFO (EBSCOhost; 1996 to present). CINAHL Complete (Cumulative Index to Nursing and Allied Health Literature; EBSCOhost; 1996 to present). We will apply the following RCT filters to identify relevant studies in the different databases. Ovid MEDLINE: Cochrane highly sensitive search strategy, as described in the Cochrane Handbook for Systematic Reviews of Interventions [ 49 ]. Embase: Cochrane RCT filter for Embase.com (version for searchers; 2023 revision; https://sites.google.com/a/york.ac.uk/issg-search-filters-resource/home/rcts/embase-rct-filter ). CINAHL: Scottish Intercollegiate Guidelines Network (SIGN) filter for CINAHL Plus with Full Text ( https://www.sign.ac.uk/using-our-guidelines/methodology/search-filters/ ). PsycINFO: Canada's Drug Agency Search Filters Database RCT/controlled clinical trial (CCT) filter for PsycINFO (EBSCO) ( https://searchfilters.cda-amc.ca/link/121 ). We will deduplicate results in EndNote with the program's inbuilt duplicate finder before exporting them to Covidence for screening. Searching other resources We will search the following clinical trials registries to identify unpublished and ongoing trials. US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov ( https://clinicaltrials.gov/ ). WHO International Clinical Trials Registry Platform ( https://trialsearch.who.int/ ). Ongoing trials that may be eligible for inclusion will be listed in the 'Characteristics of ongoing studies' table. We will search the reference lists of identified studies and narrative reviews for additional citations. With the final list of articles selected for inclusion, we will perform forwards and backwards citation searching using the SpiderCite tool [ 50 ]. We will exclude retracted publications and those with significant errata. In these cases, we will record the reason for exclusion in the 'Characteristics of excluded studies' table. To identify publications with errata or retracted publications, we will search publisher websites, PubMed ( https://www.ncbi.nlm.nih.gov/pubmed ), and the Retraction Watch database ( https://retractiondatabase.org/ ). Data collection and analysis Review authors who have been directly involved in the conduct, analysis, or publication of potentially eligible studies will abstain from decisions about eligibility, will not undertake data extraction, and will not perform risk‐of‐bias and GRADE assessments for that study. Selection of studies We will adhere to the guidance in Chapter 4 of the Cochrane Handbook for Systematic Reviews of Intervention s [ 49 ]. Two review authors will independently screen deduplicated titles and abstracts retrieved by electronic searches using a piloted screening checklist in Covidence [ 51 ]. Full‐text reports of potentially eligible studies will be obtained and independently screened by two review authors. We will resolve disagreements that arise at any stage through discussion or by consulting a third review author. We will contact study investigators for further information to aid our decision‐making as required. If these attempts are unsuccessful, we will categorise the study as awaiting classification. We will collate multiple publications of the same study under a primary study record, defined as the first publication reporting the study's primary endpoint. We will check for any postpublication amendments, including errata, corrigenda, and retractions. We will report the results of the study selection process using a PRISMA flow diagram [ 45 ], and we will record and report reasons for excluding studies at the full‐text review stage in the 'Characteristics of excluded studies' table. Data extraction and management Prior to data extraction, we will create and pilot a data extraction form, testing it on two studies within the review author team. Two review authors will independently extract study data and perform a cross‐check, resolving any differences in extracted data by discussion or by consulting a third review author. We will import the extracted data into RevMan [ 52 ]. We will record the following information, where available, in a 'Characteristics of included studies' table. Source: citation, authors' names, study name if applicable, year of publication, country, contact details. Methods: study design, recruitment procedure, recruitment setting(s), total duration of study, number of study centres and locations, study start and end dates, dates of first and last participants recruited. Participants: inclusion and exclusion criteria, reasons for exclusion, number of participants randomised, number per study arm, definition of current smoking, demographic characteristics (mean age, age range, sex, ethnicity), mean cigarettes per day, pack‐year smoking history, duration of smoking (years), mean nicotine dependence (e.g. Fagerström Test for Nicotine Dependence (FTND) score or Heaviness of Smoking Index (HSI)), motivation to quit, PROGRESS‐Plus variables (Place of residence (urban vs. rural), Race/ethnicity/culture/language, Occupation (working, retired, unemployed), Gender or sex, Religion, Education, Socioeconomic status, Social capital, age, sexual orientation, disability, homeless). Interventions: description of intervention(s) in each study arm (treatment type, dosage, number and duration of sessions, who provided the intervention, intensity, follow‐up support), what comparisons were carried out between which groups, concomitant medications, excluded medications. Outcomes: primary and secondary outcomes of interest, definition of abstinence (e.g. biochemically verified), abstinence rate at longest follow‐up time point, type of biochemical validation (if any), definition of smoking reduction, proportion of participants with follow‐up data, follow‐up length, timing of follow‐up assessments, intention‐to‐treat (ITT) and per‐protocol analysis data, adverse events and serious adverse events. Results (for each outcome of interest): sample size, missing participants, summary data for each arm, estimate of effect with confidence interval (CI) and P value, subgroup analyses. Risk of bias: see Risk of bias assessment in included studies . Miscellaneous: funding source, author declared or potential conflicts of interest, additional comments. We will contact study authors to obtain additional information as needed. If multiple records of a single eligible study contain inconsistent information, we will contact the study authors for clarification. If we receive no response after two contact attempts, two review authors will discuss the discrepancy and decide which information to include. We will note the discrepancy in the 'Characteristics of included studies' table. Risk of bias assessment in included studies Two review authors will independently assess risk of bias in the included studies using the Cochrane risk of bias tool (RoB 2) [ 53 ], as described in Chapter 8 of the Cochrane Handbook for Systematic Reviews of Interventions [ 53 ]. RoB 2 covers the following domains. Bias arising from the randomisation process. Bias due to deviations from intended interventions (here the effect of interest is assignment to the intervention at baseline (the ITT effect)). Bias due to missing outcome data. Bias in measurement of the outcome. Bias in selection of the reported result. The risk of bias assessment will cover our critical outcomes only. We will rate each domain as having a low risk of bias, some concerns, or high risk of bias for each critical outcome. We will support the rating of each domain with a brief description in the risk of bias table. We will summarise risk of bias for each outcome within a study by considering all domains relevant to the outcome (i.e. both study‐level entries, such as allocation sequence concealment, and outcome‐specific entries, such as blinding). We will provide a figure to summarise the risk of bias. For cluster‐randomised studies, we will use the relevant version of RoB 2, which includes an additional domain: bias arising from the timing of identification or recruitment of participants in a cluster‐randomised trial [ 54 ]. We will use the RoB 2 Template and Excel tool to complete and collate assessments. Two review authors will independently assess each domain using the RoB 2 series of signalling questions and answers (yes, probably yes, no information, probably no, no) and recording information for each study. Domain‐level risk of bias will be guided by responses to the signalling questions and RoB 2 algorithms, leading to judgements of low risk of bias, some concerns, or high risk of bias. Two review authors will determine an overall risk of bias judgement for included studies, resolving any disagreements by discussion or by consulting a third review author. As per Cochrane guidance, we will consider a study at high risk of bias overall if at least one domain is judged to be at high risk of bias, of low risk of bias overall if all domains are judged to be of low risk of bias, and of unclear risk for all other scenarios. Measures of treatment effect We will calculate risk ratios (RRs) and 95% confidence intervals (CIs) for dichotomous outcomes on an ITT basis (i.e. analysing participants according to the group they were originally assigned to). We will assume that participants lost to follow‐up have continued smoking. We will calculate the RR for smoking abstinence using data from the end of the intervention and longest reported follow‐up. For all other dichotomous variables, we will use the longest reported follow‐up data. For smoking abstinence, an RR greater than 1 indicates more people have quit in the treatment group than in the control group. Deaths will be excluded from the total sample size for all analyses except for adverse events. We will note adverse events, serious adverse events, and deaths in the 'Results' section of the review. If sufficient data are available, we will conduct a meta‐analysis of the incidence of adverse events and serious adverse events, using the number of participants randomised as the denominator. We will conduct sensitivity analyses, restricting the denominator to participants known to have taken at least one dose of treatment/intervention. For continuous outcomes (e.g. reduction in cigarettes per day), we will calculate the MD with 95% CI where studies report the measures on the same scale, and SMD with 95% CI where they do not (control group mean − intervention group mean)/(pooled standard deviation). We will ensure that higher scores for continuous outcomes have the same meaning for the particular outcome. We will explain the direction, and will report if we have to reverse the direction for any studies. Unit of analysis issues For individually randomised trials, the unit of analysis will be the individual participant. If we identify and include any cluster‐randomised trials, the unit of analysis will be the centre or the cluster (whichever is more appropriate). For eligible cluster‐randomised trials, we will assess whether study authors have adjusted for clustering, and whether this affected the overall result. When clustering appears to have had little impact on the results, we will use unadjusted outcome data. When clustering does appear to have affected the results, we will adjust for this using the intraclass correlation coefficient (ICC) where reported in the paper. If the ICC is not reported, we will attempt to identify an ICC from a similar study. If an ICC cannot be identified, we will not adjust for clustering but will remove the study in a sensitivity analysis. We will adjust the effective sample size by accounting for the number of clusters randomised, total participants, and average cluster size. We will calculate the effective sample size of groups in each cluster trial as the original sample size divided by the 'design effect'. We will calculate the cluster design effect as '1 + (M − 1) ICC', where M represents the average cluster size. For dichotomous data, we will divide both the total number of participants and the number experiencing the event by the same design effect. For continuous data, only the sample size is reduced, and the means and standard deviations stay the same. If cluster‐randomised trials are included, we will conduct sensitivity analyses with and without the adjustment for clustering to assess the robustness of the results, and acknowledge any limitations [ 54 ]. In studies where results are presented for multiple follow‐up periods, we will analyse the longest follow‐up period. For multiarm trials, we will identify which intervention groups are relevant to our systematic review and which specific meta‐analysis they belong to. We will make separate pairwise comparisons for the intervention of interest against each comparator. To avoid double‐counting participants, when separate comparisons with the same participants from a trial are included in a meta‐analysis of the same overall outcome, we will divide the number of participants in the intervention of interest by the number of comparisons [ 55 ]. Dealing with missing data In the case of missing data, or where the full text of a study cannot be located or is an abstract only, we will contact the study author for more information. If the information is unobtainable, and the missing data pose a serious risk of bias, we will analyse only the available data and perform a sensitivity analysis to assess the impact of including the study in this review. We will consider whether the data are likely to be missing at random. Data missing at random are less likely to result in serious bias than data not missing at random [ 56 ]. Where data are only presented for participants who were available at follow‐up, and imputation is unfeasible, we will analyse outcomes using available‐case analysis. We will note whether the study authors use imputation methods. We will note high attrition or differential follow‐up between groups. Where available, we will note sensitivity analyses using different assumptions about missing data, and whether these analyses affected the findings. We will conduct ITT analyses for all dichotomous variables, using ITT estimates as reported in each paper. If ITT estimates are not available, we will attempt to calculate the RR assuming participants who drop out or are lost to follow‐up continue to smoke. Reporting bias assessment Provided there are at least 10 studies included in a single meta‐analysis, we will assess reporting bias using funnel plots [ 57 ]. Greater plot asymmetry represents a higher risk of reporting bias. We will search for and report studies that we know were completed but for which results are unavailable. If we observe evidence of small‐study effects, we will perform sensitivity analyses according to regression‐based adjustment methods. Synthesis methods The primary analysis will include all eligible studies. If sufficient clinically similar studies are available, we will perform meta‐analyses. Studies will be listed alphabetically by study ID. We will use a random‐effects model, as we expect there will be clinical diversity. To estimate between‐trial variance, we will use the restricted maximum likelihood (REML) estimator. We will use the Hartung‐Knapp‐Sidik‐Jonkman method to calculate CIs for meta‐analysis effect estimates when there are at least three studies, and the estimate of heterogeneity is greater than zero. In other scenarios (i.e. in pooled analyses of two studies, or where the estimate of heterogeneity is equal to zero), we will use the Wald‐type method. For any studies where we cannot statistically synthesise data, we will follow the Synthesis Without Meta‐analysis (SWiM) guidelines, which include standardised data extraction techniques, estimations of common effect sizes where applicable, vote counting of the direction of effect, and assessments of study quality and heterogeneity [ 58 ]. Investigation of heterogeneity and subgroup analysis We will consider subgroup analyses to answer specific questions about particular participant groups and interventions. To limit the risk of false‐negative and false‐positive significance tests, we will limit subgroup analyses to the following, where data allow. Subsets of participants: within‐study subgroup analyses require participant‐level data. If data are available from original study authors, we will undertake subgroup analyses for sex (female/male) and LDCT scan result (negative/low‐risk nodule vs high‐risk nodule/cancer, as defined by the original papers). Subsets of studies: where data allow, we will perform between‐study subgroup analysis of more intense versus less intense behavioural support. There is no accepted threshold that defines more versus less intensive behavioural support. Hartmann‐Boyce and colleagues examined number of contacts, duration of each contact, and length of programme as intensity variables in a continuous (not categorical) model that assumed linearity. Increasing each behavioural support variable was associated with modestly increased chances of success, though effect estimates included no difference [ 47 ]. A meta‐analysis of telephone support for smoking cessation found no statistically significant differences between subgroups of low‐, medium‐, and high‐intensity telephone counselling (≤ 2 sessions: RR 1.22, 95% CI 1.02 to 1.46; 3–6 sessions: RR 1.38, 95% CI 1.17 to 1.63; ≥ 7 sessions: RR 1.49, 95% CI 0.98 to 2.25) [ 59 ]. For the purpose of this review, we will follow the categorical definition proposed by Williams and colleagues: intensive interventions consist of at least three behavioural counselling sessions, and non‐intensive interventions consist of up to two behavioural counselling sessions or provision of information online or take‐home materials such as pamphlets [ 19 ]. We will examine subgroup heterogeneity using a standardised test for heterogeneity across subgroups (e.g. Chi 2 test) and subgroup differences using the I 2 statistic in RevMan [ 52 ]. Equity‐related assessment Most LCS trials have been conducted in high‐income countries with predominantly white/European descent participants. We will not undertake a formal analysis of health inequity in this review, but will extract equity data and discuss our findings. Sensitivity analysis To examine the robustness of our results and assess the impact on effect size, we will perform sensitivity analyses limited to studies with low risk of bias (i.e. excluding studies with missing data likely to induce serious risk of bias, and studies at an overall high risk of bias). We will explore the impact of restricting the denominator of the main analyses to those participants known to have completed the treatment/intervention. If we include cluster‐randomised trials, we will conduct sensitivity analyses with and without the adjustment for clustering. Certainty of the evidence assessment We will use GRADEpro GDT software to create summary of findings tables [ 60 ]. Two review authors will independently assess the certainty of the evidence for the included outcomes using the five GRADE considerations (risk of bias, inconsistency, indirectness, imprecision, and publication bias), resolving any disagreements by discussion or by consulting a third review author [ 61 ]. We will justify all decisions to downgrade the certainty of the evidence. For our critical outcome of smoking abstinence at six months and important outcome of adverse/serious adverse events at six months, we will focus on the following comparisons. Pharmacotherapy plus behavioural versus control. Pharmacotherapy versus control. Behavioural versus control. We will conduct the review according to the published protocol. We will describe any deviations from it in detail in the 'Differences between protocol and review' section of the review. Consumer involvement Consumers (patient advocates and policy experts) are involved as co‐authors of this review. Supporting Information Supplementary materials are available with the online version of this article: 10.1002/14651858.CD016184. Supplementary materials are published alongside the article and contain additional data and information that support or enhance the article. Supplementary materials may not be subject to the same editorial scrutiny as the content of the article and Cochrane has not copyedited, typeset or proofread these materials. The material in these sections has been supplied by the author(s) for publication under a Licence for Publication and the author(s) are solely responsible for the material. Cochrane accordingly gives no representations or warranties of any kind in relation to, and accepts no liability for any reliance on or use of, such material. Supplementary material 1 Search strategies CD016184-SUP-01-searchStrategy.html (45.3KB, html) New Additional information Acknowledgements We thank Alison Manley, MLIS (Saint Mary's University, Halifax, NS, Canada) for peer review of the submitted search strategy. Editorial and peer‐reviewer contributions The following people conducted the editorial process for this article: Sign‐off Editor (final editorial decision): John C Ruckdeschel, Fox Chase Cancer Center. Managing Editor (selected peer reviewers, provided editorial guidance to authors, edited the article): Alan Thomas, Cochrane Central Editorial Service. Editorial Assistant (conducted editorial policy checks, collated peer‐reviewer comments and supported editorial team): Lisa Wydrzynski, Cochrane Central Editorial Service. Copy Editor (copy editing and production): Julia Turner, Cochrane Central Production Service. Peer‐reviewers (provided comments and recommended an editorial decision): Chukwuemeka Prince, MBBS University of Nigeria Teaching Hospital (clinical/content review); Tom Patterson, Cochrane Evidence Production and Methods Directorate (methods review); Jo Platt, Cochrane Central Editorial Information Specialist (search review). Contributions of authors Protocol design: HM (lead), HB, KM, NH, JW, GC, AF, SA, CR, MB, SL, CG, IY, KF
Search strategy: JW (lead), HM, HB, KM, NH, GC, AF, SA, CR, MB, SL, CG, IY, KF Declarations of interest HM: National Health and Medical Research Council (Grant / Contract), National Health and Medical Research Council (Independent Contractor ‐ Other), AstraZeneca Australia (Independent Contractor ‐ Other), Boehringer Ingelheim (Independent Contractor ‐ Other), Thoracic Society of Australia and New Zealand (Independent Contractor ‐ Other), Cancer Council Victoria (Independent Contractor ‐ Other), International Association for the Study of Lung Cancer (Independent Contractor ‐ Other), Department of Health and Ageing, Australian Government (Independent Contractor ‐ Other), National Health and Medical Research Council (Independent Contractor ‐ Other)
HB: no relevant interests
KM: no relevant interests
NH: no relevant interests
JW: no relevant interests
GC: no relevant interests
AF: Lung Foundation Australia (Independent Contractor ‐ Other)
SA: no relevant interests
CR: no relevant interests
MB: Lung Foundation Australia (Employment)
SL: no relevant interests
CG: The University of Queensland (Employment), BMJ (Tobacco Control) (Independent Contractor ‐ Other)
IY: is a Cochrane editor but was not involved in the editorial process for this protocol
KF: is a Cochrane editor but was not involved in the editorial process for this protocol Sources of support Internal sources Internal funding, Other No internal sources of support received. External sources External funding, Other No external sources of support received. Registration and protocol Cochrane approved the proposal for this review in June 2024. Data, code and other materials Data sharing is not applicable to this article as it is a protocol, so no datasets were generated or analysed. References 1. Sung H, Ferlay J, Siegel RL, Laversanne M, Soerjomataram I, Jemal A, et al. Global cancer statistics 2020: GLOBOCAN estimates of incidence and mortality worldwide for 36 cancers in 185 countries. CA: A Cancer Journal for Clinicians 2021;71(3):209-49. [DOI: 10.3322/caac.21660] [ DOI ] [ PubMed ] [ Google Scholar ] 2. Bonney A, Malouf R, Marchal C, Manners D, Fong KM, Marshall HM, et al. Impact of low-dose computed tomography (LDCT) screening on lung cancer-related mortality. 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