In 2017, the Global Burden of Diseases, Injuries, and Risk Factors Study found that globally, the second leading risk factor for disability adjusted life years was smoking [1], closely following high systolic blood pressure among the factors considered. Smokers are at higher risk of contracting several noncommunicable diseases, including cancer, diabetes, and cardiovascular and respiratory diseases. Despite strong evidence for the negative consequences of smoking, it continues to be a legal substance that harms and kills many individuals when used as intended by manufacturers [2].

A steady decline of the smoking prevalence in Sweden has been recorded over the past decade [3]. The most recent data from 2018 indicate that the prevalence rate was as low as 7% in the general population, lower than the 12% prevalence rate of daily use of snus (a type of tobacco placed under the lip), but higher than vaping, which is only used by 0.6% of Swedes on a daily basis [4]. This means that we are closer than ever to eradicating one of the most important causes of disease in Sweden. However, as there still are smokers and young individuals still start smoking, there is a need for effective smoking cessation interventions that can scale to a national level and that are designed to reach individuals requiring smoking cessation support in the general population.

Mobile phone–based interventions such as text messaging interventions could potentially have far reach among those who may benefit, in particular due to their reliance on standard technology and the high mobile phone ownership in Sweden. Typically, these interventions consist of a series of messages sent to participants’ mobile phones over the course of 8-12 weeks. The messages motivate participants to make a quit attempt and then reinforce and support this decision throughout the intervention period. In addition, text messaging interventions may also increase access to education and support services that promote smoking cessation [5].

Several randomized controlled trials (RCTs) have been conducted to estimate the effects of text messaging interventions for smoking cessation [5-11], notably the txt2stop trial [9] (n=5800), which found strong evidence in favor of the intervention with respect to both biochemically verified abstinence (odds ratio [OR] 2.20, 95% CI 1.80-2.68, P<.001) and self-reported abstinence (OR 1.47, 95% CI 1.40-1.66, P<.001). Three meta-analyses concluded that text messaging interventions have a positive effect on smoking cessation: One reported a summary effect size (Hedges’ g) of 0.25 (95% CI 0.13-0.38) [6], the second meta-analysis reported an overall summary OR of 1.37 (95% CI 1.25-1.51) of smoking cessation in favor of text messaging interventions [5], and the third analysis similarly found that quit rates were higher among those who had access to text messaging interventions (OR 1.36, 95% CI 1.23-1.51) [7]. Thus, there exists a relatively strong body of evidence for the average treatment effect of text messaging interventions.

In Sweden, our research group has previously conducted RCTs of smoking cessation interventions among high school [12,13] and university students [11,14-16]. Here, we found consistent evidence that a text message intervention was effective in increasing the prevalence of smoking abstinence. We are also currently conducting an RCT of a text message smoking cessation intervention tailored to patients undergoing elective surgery [17,18]. However, these interventions have recruited participants from well-defined contexts (ie, high schools, university campuses, and surgical departments) but have not taken a broader approach to recruitment in the general population. Also, there have not been any studies in Sweden of text message smoking cessation interventions targeting the general population.

The objective of this study is to estimate the effects of a text message smoking cessation intervention as a complement to treatment as usual in the general population of Sweden. In addition, the study aims to gain knowledge on the differences between individuals recruited from 2 distinct settings: online advertisement and primary health care units. In particular, the objectives of the trial are to (1) estimate the effects of a text messaging smoking cessation intervention on prevalence rates of smoking abstinence compared to individuals without access to the intervention; (2) estimate the degree to which the total effect is mediated through motivation, importance, and know-how; (3) estimate the degree to which the total effect is moderated by the mode of recruitment: online advertisements versus primary health care units; and (4) investigate differences in baseline characteristics between participants recruited through online advertisements and participants recruited through primary health care units.

A 2-arm, parallel-group (1:1) RCT will be employed to address the study objectives. The trial will follow a Bayesian group sequential design [19-21] (see Sample Size). All participants will receive treatment as usual; however, participants who are allocated to the intervention arm will also be given access to a text message smoking cessation intervention.

A timeline for participants’ progress throughout the trial is presented in Figure 1. The baseline questionnaire will assess for eligibility, and after completion, participants will be immediately randomized. The intervention period will last for 3 months, and mediator and outcome measures will be assessed at 3 months and 6 months after randomization. Mediator outcomes will also be assessed 1 month after randomization. Participation is complete after the 6-month assessment.

Allocation will be done according to a computer-generated random sequence. Prior to randomization, participants will be stratified according to which of the 2 versions of the intervention is appropriate (general or surgery). Block randomization will be used to ensure equal number of participants in each group within stratum. Random block sizes of 2 and 4 will be used in order to prevent subversion of allocation concealment.

Randomization will be done immediately after responding to the baseline questionnaire, which is done by participants on their mobile phones. Once responses are received by the backend server, automatic randomization will take place, and participants will be told about group allocation via a text message. Research personnel will not be able to affect the allocation.

Participants will be aware of their group allocation; however, research personnel will be blinded. All questionnaires are completed by participants on their own mobile phones, without supervision by research personnel. These automated procedures ensure no unblinding. Nonresponders to questionnaires will be called by phone (see Data Collection), and during this time, it is possible that participants will reveal their allocation to assessors (see Generalization and Limitations).

Baseline questionnaires will be completed by participants on their mobile phones at the time of enrollment. There are 3 follow-up intervals: 1 month, 3 months, and 6 months after randomization. All follow-ups will be initiated by sending text messages to participants with hyperlinks to questionnaires. Only mediators will be assessed at the 1-month follow-up; there will be no smoking cessation outcomes. In all cases, the following attempts will be made to collect data:

The 2 smoking cessation outcome follow-up intervals of 3 months and 6 months measure the immediate effect of the intervention and the prolonged effect of the intervention, respectively. As such, we are not proposing either to be primary above the other. Note that since our analyses are not primarily based on null hypothesis testing (see Statistical Analyses), we are not majorly concerned about the increased error rate by having multiple primary follow-up intervals.

We will use a Bayesian group sequential design to monitor recruitment with interim analyses planned every other week after the first 20 participants have completed the 6-month follow-up. Each of the primary outcomes (prolonged abstinence and point prevalence) will be modelled according to the analysis plan (see Statistical Analysis), and the coefficient for group allocation will be assessed for effect, harm, and futility. Let ß_k,i represent the regression coefficient for group allocation at time k for outcome i and D all the data currently accumulated, then the target criteria will be: p(ß_k,i > 0 | D) > 97.5% and p(ß_k,i > log(1.3) | D) > 50% for effect; p(ß_k,i < 0 | D) > 97.5% and p(ß_k,i < log(1/1.3) | D) > 50% for harm; and p(log(1/1.3) < ß_k,i < log(1.3) | D) > 95% for futility.

For the effect and harm criteria, we will use a standard normal prior for dummy covariates (mean 0, SD 1.0) and a slightly wider prior will be used for the futility criterion (mean 0, SD 2.0). The criteria should be viewed as targets; thus, at each interim analysis, we will evaluate each criterion for each covariate and make a decision if we believe that recruitment should stop or continue. However, recruitment will not exceed 24 months.

Note that this Bayesian approach allows us to look at the data an unlimited number of times without worrying about multiplicities and error rates, as would be necessary using a frequentist approach [36]. Also, since no fixed effect size is prespecified, we reduce the risk of stopping both too early and too late [21].

This trial will further our understanding of the effects of text messaging interventions among a more general population than has previously been studied. We also aim to learn about differential effects between those who seek support online and those who are given facilitated support at primary health care units.

We expect to expand upon current knowledge on how text messaging interventions may work by the investigation of mediators. The text2quit trial found that self-efficacy, know-how, and the sense that somebody cared partially mediated the intervention’s effect on smoking cessation [37]; however, there are no other similar mediator studies. Thus, the body of evidence needs to be expanded. Finally, we will also investigate for whom the interventions work by analyzing heterogenous treatment effects.

Trial recruitment is limited to the Swedish population; however, a strength of this study is the pragmatic way in which participants are recruited. Through online advertisements, individuals who decided to look for support without interference by study procedures will be recruited. At primary health care units, individuals who were not necessarily looking for smoking cessation support are given information about the trial. This closely mimics the way the intervention would be disseminated in a real-world setting and may therefore strengthen the argument of generalizability of findings.

The pragmatic design of the study aims to estimate the effects of the public health initiative as a whole (ie, recruiting participants in both online and primary health care settings). These effect estimates are also the target of our Bayesian group sequential design, which dictates the sample size. This design does however limit our ability to estimate differential effects of the 2 versions of the intervention, as well as moderating effects of the study setting. We have however decided upon this pragmatic design as it is uncertain how many participants are in need of the surgery version of the intervention, as well as the recruitment rates in the different settings, thus forming a hypothesis of the differential effect among versions and setting targets for future research.

There are well-known artifacts that arise from knowledge of participation in research that may both dilute and inflate effect estimates [38-41]; thus, these should be considered when generalizing the findings from this and other trials. Participants recruited through online advertisements are actively seeking help, and baseline assessment may therefore be an effective way for them to decide to change their behavior, diluting the effects of the intervention, as there is a ceiling limit for the intervention’s effect. Those recruited through primary health care centers are less likely to be looking for cessation support at the moment, although they may have thought about it in the past, and baseline assessment may make participants allocated to the intervention arm more receptive to the intervention than they would have been otherwise, possibly inflating effect estimates. We will have an opportunity to explore the differences between control and intervention subjects with respect to mode of recruitment to estimate these biases.

The lack of blinding of participants may introduce forms of performance bias, including both movement away and towards behavior change due to disappointment about being in the control group, and while we may hypothesize about the magnitude of this bias, we will consider it a limitation of the trial that we have no means of accounting for quantitatively.

A risk of detection bias stems from the scheme used to decrease attrition bias, by calling participants not responding to initial attempts to collect data (see Data Collection). In such a scenario, it is possible that participants disclose their group allocation to research personnel, who are otherwise blinded, during the follow-up interview. We believe that the advantage of higher follow-up rates gained by calling nonresponders outweighs this risk of bias, and personnel making the calls will be instructed to not prompt and to avoid engaging in conversation about group allocation.

Outcome measures will be self-reported, which may be susceptible to recall and social desirability bias. The Society for Research on Nicotine and Tobacco does however recommend that, in studies with limited face-to-face contact, it is neither required nor desirable to use biochemical verification [25]. Despite this recommendation, results from this trial should be understood under this limitation, as the risk of bias is exacerbated due to participants not being blinded.

While the prevalence of smoking in Sweden has decreased over the past decade, people still start smoking, and current smoking cessation aids may not be sufficient to push the prevalence further towards zero. This trial will be the first to estimate the effects of a smoking cessation text messaging intervention among both online help seekers and primary health care patients in Sweden. If effects are found to be important, then dissemination can be quick due to the trial’s pragmatic design, which may help to further reduce the smoking prevalence in Sweden.

This trial also contributes to the overall body of evidence for text messaging interventions, as it looks to increase our understanding of how effects are mediated through psychosocial variables and how effects are differential with respect to passive online recruitment and active facilitated access. Understanding how the effects of text messaging interventions are differential will help us develop more tailored and effective interventions and make support decisions about how to disseminate the interventions into real-world practice.