Effects of a text messaging smoking cessation intervention amongst online help-seekers and primary health care visitors: findings from a randomised controlled trial

Recruitment took place in two different settings. First, online advertisement (Google, Bing, and Facebook) was used to recruit individuals seeking help to quit smoking. Individuals clicking on the advert were taken to the study website which contained study information and instructions on how to sign up. Second, health care professionals at 54 participating primary health care units in the south of Sweden advertised the trial to patients through printed media (e.g. flyers, leaflets, business cards, posters). Like the website, the printed media contained study information and instructions on how to sign up. Regardless of setting, individuals were instructed sign up for the trial by sending a text message to a dedicated telephone number. Within 5 min, they received a text message in response, with a hyperlink to study information and an informed consent form.

Participants consenting to take part in the trial were immediately redirected to a baseline questionnaire, after which eligible participants were randomised. Individuals aged 18 years or older who smoked at least 1 cigarette per week were eligible for the trial. Most of the study information, and all questionnaires, were delivered to participants through their mobile phone and was in Swedish; thus, participants without access to a mobile phone and who did not comprehend Swedish well enough to sign up for the trial were excluded.

Both intervention and control groups were given treatment as usual, and neither were restricted from using other available smoking cessation aids. The intervention group were in addition given access to a text messaging intervention. Treatment as usual was in this trial defined as follows. For participants recruited through online advertisements, it was defined as referral to a nationally available smoking cessation helpline and a nationally organised website with general information about smoking and health. For participants recruited through primary health care units, it was defined as the same type of referral as participants recruited online, with additional referral from the primary health care units to have a conversation with a nurse or smoking cessation specialist about smoking cessation and health.

Two versions of the intervention were available: one general version and one that was tailored specifically for individuals undergoing elective surgery. Both versions were based on findings from our previous research [11‐13]. The elective surgery intervention was allocated to participants in the intervention group who reported having elective surgery planned in the next 3 months. Both versions of the intervention consisted of a 12-week text message program with messages sent to participants’ mobile phones daily.

Over the first few weeks, participants received 2–4 messages per day, which was reduced to 2 messages per day during the middle part of the intervention, and further reduced to 1 message per day during the latter part of the intervention. The content of the messages was primarily informational and encouraging, and some messages asked participants to do specific tasks, such as throw away ashtrays. None of the messages asked participants to respond, but participants could request extra supportive messages by sending a text message with one of three keywords: weight, relapse, or craving. A message was then sent back to participants with specific information about potential weight gain, what to do if one relapses, or help if they were experiencing nicotine cravings. Unique for the elective surgery version was that additional messages about complications and recovery from surgery were included, and some of the messages included hyperlinks to web-based modules which contained materials specifically designed for the surgery context. Please see the study protocol for more details [14].

At baseline, participants were asked to complete an electronic questionnaire on their mobile phones. The questionnaire asked about the following: gender, age, the number of years smoking, monthly/weekly/daily smokers and the number of cigarettes typically smoked in this interval, lifetime number of quit attempts, cessation counselling experience, use of quit smoking helpline, and use of snus (which is a moist oral tobacco product which is common in Sweden, sometimes translated as snuff). In addition, participants completed the Fagerström Test for Nicotine Dependence scale (FTND) [16], which scores participants from 1 to 10, where higher scores indicate higher nicotine dependence. Due to snus being commonly used in Sweden, the scale was amended to include one item asking about the use of snus. The item asked: Do you use snus?, with response options: No; A few times a month; A few times a week; Daily – less than 1/3 of a box; Daily – 1/3 of a box; Daily – 1/2 of a box; and Daily – 1 box or more. For scoring purposes, a full box per day or more scored 3 points, half a box daily scored 2 points, third of a box daily scored 1 point, and the other response options scored 0 points. The total FTND score was calculated using either the snus item or the standard cigarette item, whichever the participant scored higher on. Note that only 21 participants (2.1%) scored higher on the snus item. The internal reliability of the FTND for this sample was assessed using Cronbach’s alpha, which resulted in an alpha of 0.67. This is below what is typically considered a fair reliability for clinical purposes, although note that here we only use it to adjust our primary analyses for baseline dependence and not as an outcome measure. The FTND scale has not been validated in the context of this study; however, scores ranging between 5 and 7 have previously been used to indicate moderate nicotine dependence and 8 + to indicate high nicotine dependence.

The primary outcomes were prolonged abstinence and point prevalence of smoking abstinence, measured at 3 and 6 months post-randomisation. Prolonged abstinence was defined following the Russell standard [17] definition of not having smoked more than 5 cigarettes in the past 8 weeks (thus allowing for a 4-week grace period). The abstinence period was adjusted to 5 months at the 6-month follow-up. Point prevalence of smoking abstinence was defined as not smoking any cigarette during the past 4 weeks, as recommended by the Society for Research on Nicotine and Tobacco [18].

Secondary outcomes were 7-day point prevalence of smoking abstinence, number of cigarettes smoked weekly (if still smoking), number of quit attempts since baseline, and number of uses of other smoking-cessation aids since baseline.

Three potential mediating factors were assessed: importance, confidence, and knowledge of how to quit (know-how). To reduce participant burden across the entire trial period, we decided against using multi-item questionnaires to measure these factors, instead relying on face valid single-item measures based on importance and confidence rulers [19]. The items used are presented in Table 1. Findings from mediator analyses based on these outcomes will be reported separately; however, due to limited evidence of construct validity, caution is advised in interpreting findings based on these mediators.

There were three follow-up intervals: 1, 3, and 6 months post-randomisation. At the 1-month follow-up, the three hypothesised mediators were assessed only. All follow-ups were initiated by sending text messages to participants with hyperlinks to questionnaires. In all cases, the following additional attempts were made to collect data:

Allocation was done according to a computer-generated random sequence. Participants were stratified according to which of the two versions of the intervention was appropriate (general or surgery). Block randomisation was used to ensure equal number of participants in each group within stratum, using random block sizes of 2 and 4. Randomisation was done immediately after participants responded to the baseline questionnaire using their mobile phone. Once a response was received by the backend server, allocation took place automatically, and participants were told about group allocation via a text message. Research personnel were not able to affect the allocation and all study procedures were automated, preventing subversion of allocation concealment.

Participants were aware of their group allocation; however, research personnel were blinded. All questionnaires were completed by participants on their own mobile phones, without supervision by research personnel. Non-responders were called, and during the call, it was possible that participants revealed their allocation to assessors. This means that there was a risk of detection bias (see Limitations).

The statistical methods applied were pre-specified in the trial protocol [14]. All participants were included in the analyses in the groups to which they were randomised (intention-to-treat). Missing data was initially handled by available case analysis under the missing at random (MAR) assumption. Outcome data missing systematically due to the outcome itself will invalidate the MAR assumption; thus, evidence of such was sought in attrition analyses. Sensitivity analyses that include imputed values for missing outcome data were also conducted.

All models were estimated using Bayesian inference [20]. We use the median of the posterior distribution as a point estimate of effect and report 95% compatibility intervals (CoI) defined by the 2.5% and 97.5% percentiles of the posterior distribution. We complemented the Bayesian analyses with null hypothesis tests at the 0.05 significance level.

Descriptive statistics of primary and secondary outcomes are presented in Table 3. Posterior densities of primary outcome effect estimates are depicted in Fig. 2, and point estimates are presented in Table 4. Point estimates of effects for secondary outcomes are presented in Table 5. Overall, smoking abstinence was markedly higher in the intervention group, both at 3 and 6 months post-randomisation. This is evident when looking at the posterior densities of odds ratios in Fig. 2, as they are shifted to the right of one, and the posterior probability of effect is high in all cases in Table 4. Amongst those still smoking, the number of cigarettes smoked per week were lower in the intervention group at both follow-up intervals, and the number of quit attempts were higher in the intervention group at 3 months. There was no observed difference in use of other support between groups.

Participants were recruited online and through primary health care centres, mimicking closely how the intervention could be disseminated in the real-world. Inclusion criteria were allowing, and few participants who showed interest in the trial were excluded. This pragmatic trial design leads us to interpret findings as estimates of effectiveness rather than efficacy, which strengthens the external validity of the trial. The design did however also limit our ability to blind participants, as they were naturally aware if they received the intervention or not. Although one could imagine some form of sham intervention with text messages containing non-smoking related information, it is unlikely that this would convince those seeking help that they had received cessation support.

Attrition rates were high in this trial, as is often the case with online trials with low thresholds of participation [26]. It was easy to join the trial even if one was simply curious about the trial itself with no intention of following through and likewise easy to forget that one was participating in a trial at all. We took measures to minimise attrition by using text reminders and calling for responses when necessary, however, even these strategies cannot guarantee full follow-up. Our sensitivity analyses using imputed data did not result in findings markedly different from those using available data. While age was associated with non-response, it was not consistent across all primary outcomes and follow-up intervals, and it was not differential between groups. There was however evidence that late responders in the intervention group were more likely to be self-reported smokers than late responders in the control group. While the assumption that late responders and non-responder are more alike than early responders cannot be tested, there is still a pattern of response which may suggest that the MAR assumption does not hold. Although speculative, it may be due to social desirability, where those who received the intervention felt that they were not living up to the researchers’ expectations of them, and thus did not want to respond to the questionnaires. If so, then estimates in our trial may be inflated. However, this analysis has its own limitations in terms of decreasing sample sizes as the number of attempts increase (se Fig. 4), and the model assumption of a monotonic relationship. Nonetheless, the estimates produced using imputed data, which uses available outcome data as auxiliary to predict missing outcome data, may therefore be interpreted as more conservative estimates of effectiveness.

Outcome measures were self-reported in this trial, which may be susceptible to recall bias and exacerbate the risk of 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 [18], since it may introduce selection bias in who is tested. Lack of blinding of participants in combination with self-report does however introduce risk of performance bias, including both away and towards behaviour change due to disappointment about being in the control group [27, 28]. In addition, it is possible that those allocated to the intervention group were affected by social desirability to a greater degree than those in the control group, and therefore exaggerated their reports of non-smoking to conform to the aims of the trial, thereby biasing effect estimates away from the null.

All study procedures were automated, ensuring that the concealment of the allocation sequence could not be subverted nor that research personnel could become aware of allocation. However, to reduce attrition bias, we called participants who did not respond to our initial attempts to collect data. This induces a risk of detection bias, which has been shown to affect outcome reporting [29]. However, personnel who were making the calls were instructed to promptly ask the two primary outcome questions and collect responses and not probe participants about anything else. It is inevitable that some participants may have revealed their allocation anyway; however, we found that this risk of bias was minimal and worth taking as it decreased the risk of attrition bias.