Lottery incentives for smoking cessation at the workplace: a cluster randomized trial

Abstract

Background

Smoking is the largest behavioral risk factor for loss of healthy life years. Many smokers intend and try to quit, but have trouble realizing their behavioral health goals. When workplace cessation-support is accompanied by incentives, this can increase its effectiveness. Based on principles from behavioral economics and psychology, regret lotteries have supported the realization of other health behaviors. Regret lotteries capitalize regret aversion by always informing winners at the deadline, but withholding prizes if they smoked. This study builds on previous applications of regret lotteries to test its potential, using a novel combination of incentives, the workplace as a context and smoking as the target behavior.

Methods

We compared a workplace group cessation training (control arm) to the same training plus regret lotteries (intervention arm). To test its effect on smoking cessation, we performed a cluster randomized trial with 13 organizations and 111 participants, followed for 52 weeks. Participants in the intervention arm additionally participated in 13 weekly lotteries, followed by a long-term lottery after 26 weeks. In each lottery, winners were drawn from all participants in a group. Winners were promised to always learn the outcome of the lotteries. However, the winners could only claim their prize if they did not smoke. The primary outcome of interest was continuous smoking abstinence at 52 weeks from the quit date, self-reported and biochemically validated with a carbon monoxide measurement and a cut-off point of ≤ 9 parts per million. A multi-level logistic regression analysis was performed to estimate the treatment effects after 52 weeks, while accounting for the clustered data pattern within organizations. We adjusted for Fagerström nicotine dependence score, education level, income, age and gender. Secondary outcomes were abstinence at weeks 13 and 26 after the quit-date.

Results

At the 52-week primary outcome point of this trial, in the control arm, 23.9% of participants were continuously abstinent opposed to 43.2% in the intervention arm (OR = 3.25; 95% CI, 0.99–10.70). Thirteen weeks after the quit date, in the control arm, 35.8% of participants were continuously abstinent opposed to 68.2% in the intervention arm (OR = 3.66; 95% CI, 1.47–9.16). After 26 weeks, in the control arm, 25.4% of participants were continuously abstinent opposed to 54.6% in the intervention arm (OR = 3.24; 95% CI, 1.27–8.22).

Conclusions

Although differences were only statistically significant up to 26 weeks, we found meaningful and practically relevant increases in smoking cessation due to the lottery intervention at the main outcome point. The intervention design was rooted in behavioral economics and builds on previous successful applications. Therefore, the results show enough potential to theorize and further apply this method in a field setting, that can benefit from the theoretical, methodological and practical lessons learned in this trial.

Trial registration

The trial protocol and materials were reviewed and approved by the Radboud University Ethical Review Board (ECSW-2019–114). The study was registered in the Dutch Trial Register (trial registration number: NTR NL84632, 17 March 2020) and lottery drawings were performed by an independent notary.

Supplementary Information

The online version contains supplementary material available at 10.1186/s12889-025-25376-3.

Background

Most smokers do not want to smoke [1]. Many have tried to quit at least once in their lifetime and in order to succeed, have sought and tried multiple quit methods [2, 3]. However, most quitting attempts are unsuccessful [1]. Smoking is an addictive habit and the smoker and its broader environment need to be strong, structured and aligned with the goal of stopping to increase the chance of success. As such, there is a continuous quest for effective smoking-cessation interventions that are feasible, affordable and accessible for different socioeconomic groups [4].

Public health policies have effectively reduced smoking prevalence globally over the past decades. Smoking has become less appealing due to systemic policies such as smoking bans and tobacco taxes, especially when implemented simultaneously [5]. Nonetheless, tobacco use still accounts for 8.7 million deaths annually and remains the largest behavioral risk factor for loss of healthy life years [6]. Even when many system-level factors discourage smoking, effective assistance in quitting smoking remains necessary [7].

The workplace is a well-suited setting for the provision of cessation support for multiple reasons. First, research shows that proximity, affordability and accessibility are key elements in the uptake of cessation support, especially among disadvantaged groups [8]. The workplace is generally a physically and socially familiar context and offers an existing (financial) infrastructure for support. Second, while employers can offer interventions out a sense of shared responsibility for the health of their employees [9], they can also benefit financially from smoke-free employees. In comparison to a non-smoking employee, smoking employees have a 31% higher likelihood of absenteeism and have three more sick days annually [10]. Third, a review of the literature shows strong evidence that workplace interventions directed at individual smokers, including group counselling, can increase the likelihood of successful smoking cessation [11].

Previous studies have shown that workplace smoking-cessation interventions can benefit from the addition of financial incentives. For example, a randomized trial with 61 organizations found that a workplace cessation group training resulted in 26.4% abstinence after 12 months, whereas an additional individual €350 incentive resulted in 41.1% smoke-free participants [12]. A behavioral economic explanation for why such incentives are effective, is that they offer a short-term and noticeable decision-consequence. This in contrast to the more uncertain and delayed health benefits that come with smoking cessation. In this reasoning, accepting incentives acts as a self-commitment device: a way for people to align their immediate actions with their own long-term health goal, by redirecting their future behavior away from the immediate gratification of smoking.

In this same tradition, scholars have tested lotteries that leverage regret aversion. Regret lotteries -also named commitment lotteries- draw the winner from all participants and inform the winners of their prize. However, the winners can only claim their prize if they obtained their predefined behavioral goal. A randomized trial at the workplace with six company gyms showed that, in comparison to a control arm, weekly regret lotteries for three months combined with a six-month larger lottery resulted in higher levels of gym attendance up to 12 months [13, 14]. Beneficial results were also found for weight loss [15], and medication adherence [16]. Typical for these studies is the use of a short-term incentive with a longer-term follow-up measurement of behavior change.

By their design, regret lotteries build on multiple psychological insights on goal attainment: they offer repeated, nearby and salient deadlines, which are given their weight by the promise of counterfactual feedback about the lottery outcomes. The possibility of finding out that you could have won a prize, if only you decided differently in the past, leverages the human tendency to anticipate future regret of current decisions [17]. This way, they overcome the procrastination of lifestyle improvement, which can be rewarding in the short-term, but costly in the long-term. Despite their previous successful applications, regret lotteries remain untested in the support of smoking cessation. Therefore, this study builds on previous applications of psychologically designed lottery incentives to test its potential, using a novel combination of incentives, the workplace as a context and smoking as the target behavior.

The aim of this study was to test the effectiveness of “The Smoke-Free Lottery”. In a cluster randomized trial, we investigated whether lotteries increased the effectiveness of tobacco-cessation group training at the workplace in the short-term and the long-term. It was hypothesized that the lotteries would increase continuous abstinence rates over cessation training alone.

Methods

Study design

The rationale and protocol of this trial have been published elsewhere [4]. The design was a two-arm, parallel group, clustered-randomized trial running for 52 weeks in 13 organizations (clusters) across the Netherlands. Random allocation occurred at the organization (cluster) level. Working units within larger organizations could be allocated separately if the organizational circumstances ensured that treatment contamination could be avoided.

The trial ran from May 2020 with the first baseline measurement until February 2023, the moment of the final follow-up data collection. Organizations were randomly allocated to 1) a group receiving smoking-cessation training (control arm) or 2) a smoking-cessation training plus the smoke-free lottery (intervention arm). Figure 1 illustrates the trial flow and event schedule.

Fig. 1.

Trial flow and event schedule

Participants in both arms participated in an identical 8-week smoking-cessation group training at the workplace. Participants in the intervention arm additionally participated in 13 weekly lotteries, beginning in week 4 of the smoking-cessation training on the prespecified joint quit date, complemented with a long-term lottery after 26 weeks. Figure 2 displays the participant flow for both the intervention and control arm. The trial protocol and materials were reviewed and approved by the Radboud University Ethical Review Board (ECSW-2019–114). The study was registered in the Dutch Trial Register (NTR NL8463) and lottery drawings were performed by an independent notary. This paper adheres to the CONSORT guidelines for reporting clinical trials.

Fig. 2.

Flow of participants

Participants and enrollment

A diverse array of organizations were eligible to participate, if the management agreed to pay for the training and, if assigned to the intervention arm, to pay for the lotteries. We focused our recruitment on organizations likely to employ populations from lower socioeconomic circumstances, although participation was not limited to these organizations. Additionally, the organization’s management had to allow their employees to participate in the group training sessions and carbon monoxide (CO)-measurements (see Outcomes and measures) during or shortly before or after working hours on a location hosted by the employer. After the outbreak of Sars-Cov-2, the training was hosted online, which dismissed the location-criterion.

Participants were eligible if they indicated to have smoked tobacco (no e-cigarettes) for at least one pack-year (number of daily packs x years), smoked daily, were willing to quit, wanted to join the group training and were at least 18 years old. Employees that were not able to read or speak Dutch were excluded from participation in this study because the smoking-cessation training sessions were conducted in Dutch. Informed consent was obtained from all individual participants. As compensation for their participation in the study, participants were given €30 at the end of the study, regardless of smoking status. For more details on recruitment strategies, see Van der Swaluw et al. [4].

Intervention

Control arm

Participants joined an evidence-based group smoking-cessation training organized by the Dutch company, SineFuma, which was developed independently of this study and is based on Withdrawal-oriented Therapy [18] and Motivational Interviewing [19]. The standard SineFuma group training consisted of seven meetings of 90 min, spread over eight weeks. After two weeks of preparation and group forming, participants got a pause-week and jointly quit in the third meeting (week 4). Participants were given a personal CO meter, which they had to connect to their smartphone. Smoking status was assessed through text messages and verified by the CO measurements (see Outcomes and measures). After the outbreak of COVID-19, the training was offered as e-health training online.

Intervention arm: smoke-free lottery

Weeks 1 to 13

Participants in the intervention arm received the same smoking-cessation training as the control arm in all aspects, and additionally participated in lotteries. The lottery timeline is illustrated in Fig. 3. We offered repeated weekly short-term lottery deadlines, immediately after the target quit date in week 4 of the training. From this point, during the initial 13 lottery weeks, participants in the intervention arm could win €50 every week (see Van der Swaluw et al. [4] for the rationale behind the prize size). Each week, one winner per training group was drawn from all participants within that group using trial-ID’s by an independent notary, regardless of their current smoking status. However, winners received their prize only if they did not smoke that week, as confirmed by the text message and CO measurement, prior to the drawing. Participants were informed through text message and email about (1) whether they had won the prize, and (2) whether they would receive their prize. Therefore, winners who smoked were also informed about their forfeited prize. No additional winner was selected if the initial winner smoked. All other participants were also informed about whether the prize was awarded or not, but not to whom. During these 13 weeks, each week offered a new chance to win, regardless of prior performance.

Fig. 3.

Timeline of the lotteries

Weeks 14 to 26

The weekly lotteries ended after 13 weeks. Instead, at week 26, all participants had the opportunity to win a family vacation voucher (worth €400). Due to the outbreak of SARS-CoV-2, it was chosen and communicated to transfer the €400 to the winners’ bank account To determine eligibility for this prize, abstinence between weeks 14 and 26 was verified with aan addititional CO measurement conducted at a timepoint during this period, the exact timing of which was undisclosed to participants in advance. Again, per training group winners were drawn out of all participants within that group, regardless of their smoking status. The winner was always informed via text message and email. However, the winner only received the prize if he or she was abstinent between weeks 14 and 26, as confirmed via text messages and CO measurements. Counterfactual feedback was promised by informing participants that, if they were selected as winners but could not claim their prize because they resumed smoking, they would also be notified of this outcome. If the winner was not eligible for the prize, a new winner was drawn until the prize could be awarded. All other participants were also informed via text message and email that the prize was awarded, but not to whom.

Outcomes and measures

Primary outcome

The primary outcome of interest was continuous smoking abstinence at 52 weeks after the quit date, biochemically validated according to the Russell Standard (RS). Participants reported their smoking status weekly via text messages from the start of training (baseline) until 13 weeks after the quit date, as well as at weeks 26 and 52. The outcome points of 13 and 26 weeks were chosen such that we could assess results at the end of each lottery-period. The outcome point at week 52 was chosen to also measure the potential long-term effectiveness of the intervention.

Smoking status was verified using the iCOquit Smokerlyzer® (Bedfont Scientific Ltd). Each participant received a personal device that could be connected to their smartphone, allowing CO measurements to be sent directly to the study staff through the accompanied app. Participants completed weekly CO measurements up to 13 weeks after the quit date, as well as scheduled measurements at weeks 26 and 52. In addition, participants were informed that there would be one unannounced (‘surprise’) measurement between weeks 14–26, but they were not told the exact timing of this measurement in advance. We used the Russell Standard (RS) to evaluate abstinence [20]. Following the RS, we applied the following criteria: first, a cut-off point of ≤ 9 parts per million (p.p.m.) was used to determine smoking status; second, discrepancies between self-reported and biochemical data or non-responses were assumed to indicate smoking; and third, participants were considered abstinent if they reported smoking no more than five cigarettes between the quit day and week 52 and verified their abstinence biochemically at week 52.

Covariates

At the baseline measurement, which was at enrollment to the study, participants filled out a survey. Demographics (age, gender, education level, and income), and nicotine dependence (translated Fagerström Test for Nicotine Dependence (FTND [21])) were covariates (see van der Swaluw et al., 2023). Participants were asked to report their highest level of education, which was categorized into three strata: low (no education, primary, or lower secondary education), moderate (middle secondary education), and high (upper secondary and university education). Income was categorized in tertiles, with 0–2000 monthly personal net income in euro classified as low, 2000 to 4000 as middle and 4000 and up as high.

Sample size and randomization

Anticipating a 0.35 difference between proportions in smoking cessation, based on a meta-analysis by Haff et al. [16], and accounting for the clustered design, we estimated a required sample size of 54 per arm and aimed to include at least 64 participants per arm, allowing for 15% attrition over time. Based on our power calculation with an estimated cluster size of 8, we aimed to assign 16 clusters in total to receive either a smoking-cessation training alone or a smoking-cessation training plus the smoke-free lottery.

Organizations (clusters) were randomized using a computer-generated biased urn schedule prior to the recruitment of individual participants. Due to the sequential inclusion of organizations, the biased urn method entailed that the allocation probability changed based on the current balance [22]. Larger organizations with multiple autonomous working units (e.g. departments) could be randomized separately, provided treatment contamination could be avoided. Allocation concealment at the organization level was ensured by first including the organization and randomizing after the organization agreed to participate. Participants were not informed about the lottery in the other arm; however, blinding could not be fully guaranteed due to the public nature of the organization's recruitment and the nature of the lottery-treatment.

Statistical analyses

Participants were the primary unit of inference in all analyses. Analyses followed the intention-to-treat principle, meaning that all randomly assigned participants were included in the denominator for calculating abstinence, in accordance with the Russell Standard. Statistical significance was set at p < 0.05. Analyses were conducted using R version 4.4.0. Planned analyses can also be found in the trial protocol [4].

Primary outcome

Analysis of the primary outcome examined the difference in continuous smoking abstinence between intervention arm and control arm 52 weeks after the quit date. A multi-level logistic regression analysis was performed to estimate the treatment effects at 52 weeks, while accounting for the clustered data pattern within organizations. The verified continuous abstinent status of each participant was used as the dependent variable and the allocation group and covariates as the independent variables. Random intercepts were added at the organization level to account for clustering of observations within organizations.

We adjusted for Fagerström nicotine dependence score, medication used for quit attempt (yes, no) education level, income, age and gender (see Table 1). Missing data on covariates were imputed using the variables in the model. We created 50 complete datasets using the mice package in R, with the maximum number of iterations set to 20. Convergence of the mice algorithm was visually checked.

Table 1.

Baseline participant characteristics displayed by study arm

		Control arm (n = 67)	Intervention arm (n = 44)
Age (mean (SD))		47.5 (10.4)	46.4 (11.5)
Sex (%)	Male	42 (62.7)	22 (50.0)
	Female	25 (37.3)	22 (50.0)
Educational level (%)	Low	8 (11.9)	2 (4.5)
	Middle	16 (23.9)	14 (31.8)
	High	21 (31.3)	24 (54.5)
	Missing	22 (32.8)	4 (9.1)
Income level (%)	Low	6 (9.0)	5 (11.4)
	Middle	32 (47.8)	33 (75.0)
	High	5 (7.5)	0 (0.0)
	Missing	24 (35.8)	6 (13.6)
Fagerström test for nicotine dependence (mean (SD))		4.21 (2.02)	3.72 (1.61)
	Missing	14 (20.9)	5 (11.4)
Used medication for quit attempt	Yes	44 (65.7)	18 (40.9)
	No	22 (32.8)	24 (54.5)
	Missing	1 (1.5)	2 (4.5)

Secondary outcomes, and sensitivity analyses

Secondary outcomes included smoking cessation according to the RS at 13 and 26 weeks after the quit date. Multi-level logistic regression analyses estimated the treatment effects at 13 and 26 weeks, while accounting for the clustered data pattern. The verified continuous abstinent status of each participant at weeks 13 and 26 respectively was used as the dependent variable and the allocation group and covariates as the independent variables. As sensitivity analyses, the models were also run with a cut-off point of ≤ 6 parts per million instead of 9 p.p.m for biochemical validation [23].

Results

Thirteen organizations were recruited from January 2020 to February 2022, resulting in a total of 111 participants. All clusters were randomly assigned to either the intervention arm (7 clusters, 44 participants) or the control arm (6 clusters, 67 participants), see Table 1. In the intervention arm, participants had a mean age of 46.4 (SD = 11.5) years, with an equal distribution of male and females. The majority of participants in this group were higher educated and had a middle income level. In the control arm, the mean age of the participants was 47.5 (SD = 10.4) years, with the majority being male (62.7%). Similar to the intervention arm, most participants in the control arm had a high educational level and a middle income level. The mean Fagerström score was 3.7 for the intervention arm and 4.2 for the control arm. In the control arm, 65.7% of participants used medication to quit, whereas 40.9% in the intervention arm did.

In the control arm, the mean number of attended smoking-cessation trainings was 5.64 (SD = 2.36) out of seven. In the intervention arm, the mean number of attended group-cessation trainings was 6.64 (SD = 1.17) out of seven.

Continuous smoking abstinence

Table 2 displays per study arm and for each period the number of smoke free participants, both self-reported and biochemically validated. Discrepancies between self-reported and biochemical data or non-responses were assumed to indicate smoking.

Table 2.

Continuous smoking abstinence per study period

	Control arm	Intervention arm
	N = 67	N = 44
13 week abstinence
Self-reported (%)	30 (44.8)	33 (75)
Biochemically validated (%)	24 (35.8)	30 (68.2)
26 week abstinence
Self-reported (%)	27 (40.3)	26 (59.1)
Biochemically validated (%)	17 (25.4)	24 (54.6)
52 week abstinence
Self-reported (%)	24 (35.8)	20 (45.5)
Biochemically validated (%)	16 (23.9)	19 (43.2)

Unadjusted frequencies of continuous smoking abstinence

Thirteen weeks after the quit date, participants in the intervention arm were more likely to have been continuously abstinent than participants in the control arm. In the control arm, 35.8% of participants were continuously abstinent for 13 weeks opposed to 68.2% in the intervention arm (Fig. 4). Accordingly, the mixed logistic model (Table 3) showed a statistically significant intervention effect on smoking cessation for the intervention arm (OR = 3.66; 95% CI, 1.47–9.16, p < 0.01).

Fig. 4.

The proportion of biochemically validated abstinent participants at each endpoint. Unadjusted biochemically validated continuous smoking abstinence according to the Russell Standard

Table 3.

Logistic mixed models predicting continuous abstinence

		Weeks 13	Week 26	Week 52
		Odds ratio (95% CI)	Odds ratio (95% CI)	Odds ratio (95% CI)
Study arm
Control (ref.)
Intervention		3.66 (1.47–9.16)**	3.24 (1.27–8.22)*	3.25 (0.99–10.70)
Participant characteristics
Age		1.04 (1.00–1.08)	1.03 (0.99–1.08)	1.05 (1.00–1.09)*
Sex
	Male (ref)
	Female	0.52 (0.19–1.42)	0.75 (0.27–2.05)	1.26 (0.45–3.53)
Fagerstrom score		0.91 (0.70–1.17)	0.85 (0.65–1.12)	0.94 (0.71–1.24)
Education
	Low (ref)
	Middle	1.53 (0.38–6.15)	1.78 (0.39–8.08)	1.46 (0.33–6.51)
	Higher	2.20 (0.53–9.20)	2.79 (0.60–12.99)	1.56 (0.34–7.18)
Income
	Low (ref)
	Middle	0.47 (0.11–2.14)	0.29 (0.06–1.32)	0.62 (0.14–2.78)
	Higher	0.19 (0.02–1.88)	0.13 (0.01 −1.48)	0.15 (0.01–2.57)

Intracluster correlation (ICC) (Week 13): 0.00, (Week 26): 0.01, (Week 52): 0.09

Intention-to-treat analyses with multiple imputation on missing variables

^*Significant at p <.05; **Significant at p <.01

After 26 weeks, participants in the intervention arm were more likely to be continuously abstinent than participants in the control arm. In the control arm, 25.4% of participants were continuously abstinent for 26 weeks after the quit date opposed to 54.6% in the intervention arm (Fig. 4). The mixed logistic model (Table 3) showed a statistically significant intervention effect on smoking cessation for the intervention arm (OR = 3.24; 95% CI, 1.27–8.22, p = 0.01).

At the 52-week primary outcome point of this trial, in the control arm, 23.9% of participants were continuously abstinent opposed to 43.2% in the intervention arm (Fig. 4). This difference was not statistically significant at the less than 0.05 level (odds ratio [OR] = 3.25; 95% CI, 0.99–10.70; p = 0.05) (Table 3).

Sensitivity analyses

When we tested the cut-off point of ≤ 6 parts per million instead of 9 p.p.m for biochemical validation [23], the percentages of verified abstinence changed only slightly. This did not lead to different magnitudes or significance levels in the regression models (see Appendix Table 1). When we entered medication use (yes, no) as an additional covariate, this also did not lead to notable different effect sizes nor significance levels in the regression models (see Appendix Table 2)

Discussion

Although statistically significant outcomes were only observed at 13 and 26 weeks, the findings from this cluster randomized trial demonstrate practically important effects of the lottery intervention on smoking cessation up to 52 weeks, with statistically significant outcomes observed at 13 and 26 weeks. The present findings also expand knowledge on the use of commitment devices to facilitate behavior change. Previous studies tested regret lotteries in different settings and for different health behaviors. They found that regret lotteries supported gym attendance [13, 14], weight loss [15], medication adherence [16] and vaccination [24]. In the same tradition, behavioral economic incentives for smoking cessation have shown positive effects on cessation rates. Adding to this body of literature in a novel setting, we find a substantial increase in cessation in the randomized lottery treatment. Due to its theoretical underpinning and previous successful applications in the broader behavioral health economics literature, further development is promising.

Practical relevance of effect sizes

Most unassisted quit attempts are unsuccessful, with about 5% of smokers achieving their behavioral health goal [25]. At the main outcome point in this trial, we find a 19.3 percentage point difference in success due to the regret lotteries, 52 weeks after participants quit smoking. A relevant question is whether any effect size within the confidence interval is substantial enough to hold practical relevance, despite not reaching the statistical significance threshold [26]. We interpret our findings accordingly, to ensure that clinically relevant findings might not be overlooked.

Statistical significance depends on both the effect size and the sample size. In a discussion paper, Troxel and Volpp quantitatively demonstrated that cessation trials using incentives with lower sample sizes could have a potential substantial public health effect, despite their non-significant result [27]. The combination of substantial differences between arms and lower sample sizes could lead to the too bold conclusion that the incentive did not work. They calculate that many trials in their review did not have enough power to detect even a threefold increase in cessation rates between arms. They compare results of a larger trial to those of smaller trials (N = 47–175) included in an existing Cochrane review of financial incentives for smoking cessation in a workplace setting. They conclude that many studies were underpowered to detect effects. This might be true for the present trial. They summarize their findings by the common maxim that absence of evidence does not mean evidence of absence.

We performed an ex-ante sample size calculation with assumptions based on existing literature about clustering, cluster size and attrition [4]. In our trial, we did not manage to recruit the 16 anticipated organizations and 128 calculated number of participants. Largely due to the pandemic. In addition, in hindsight, our approximated difference between proportions could have been more conservative. For example, an incentive-trial in a similar context (group training at a workplace setting in the Netherlands) found a similar difference between arms at the main outcome point 52 weeks after the quit date (~ 15%, versus ~ 19% in this trial) [12]. Yet, the prior trial had about 5 times as many organizations included and also found statistically significant differences. Future trials testing variations of regret lotteries for smoking cessation can build on the present trial in estimating the effect size and should include more organizations and participants.

Short-term versus long-term behavior change

Our analysis reveals a pattern in which odds ratios (ORs) remain consistent over time, while the confidence intervals (CIs) widen after the intervention ended. This observation may suggest that, in the absence of an active intervention during the follow-up period, other contextual factors increasingly influenced the ability for participants to remain smoke free. Without the intervention, some participants might have had supporting social and physical environments to maintain their behavior change, while others were challenged more. This heterogeneity in maintenance should be part of future intervention development.

We based the front-loaded schedule of the incentive, meaning that proportionally more incentives are provided at the beginning of the intervention, on multiple insights about the pathways of smoking cessation and relapse [4]. First, success in the early stages of quitting is most predictive of long term success [28]. Second, the probability of relapse plateaus after 26 weeks, suggesting that most support is needed in the first six months of quitting [29]. Nevertheless, our results have not yet reflected the anticipated impact of applying these insights to interventions. Indeed, psychological theory shows that behavioral initiation differs from behavioral maintenance [30]. Preventing relapse might need different intervention components than promoting inhibition [31]. If the different stages of a smoke-free life come with different challenges, support in context and interventions could be tailored to this.

Incentive design matters

Meta-analyses [32] and choice-experiments [33] show that the design of incentives matters for its uptake and effects. However, in many trial descriptions, the rationale behind the design of incentives is not described nor profiting from the recent practical insights of behavioral economics [34]. For example, a review studying incentives for smoking cessation concluded that higher incentive amounts do not lead to greater quit rates, suggesting that other, unidentified design features might have influenced differences in outcomes [35]. Notwithstanding its theoretical potential and despite good examples, the current body of literature does not yet lead to an unequivocal proposal for how to optimally use behavioral economics in the design of incentives for smoking cessation support. More real-world examples, building on existing evidence, could support the quest for effective and attractive cessation programs.

For this reason, we field-tested lottery-incentives with a strong behavioral economic foundation, leveraging regret aversion. Existing overviews of the literature showed little promise of traditional lotteries for smoking cessation [36]. However, in contrast to traditional quit-and-win contests, the regret lotteries tested in this trial differed in key aspects [4]. First, in previous interventions, the reward for cessation was a lottery ticket. Remaining smoke-free provided access to the drawing. As such, the lottery tickets were an uncertain pay for performance, as both eligibility and winning were uncertain. In the present trial, lottery participation was guaranteed: all participants were in every drawing. While the outcome of winning remains uncertain, the opportunity to participate is not tied to performance. Second, in a traditional lottery intervention, unsuccessful participants never learned what would have happened if they were smoke-free at the time of the drawing. As a result, they could not anticipate the regret of finding out that their ticket has won the prize, while not being eligible to claim it. It is this anticipating form of precommitment through regret that we emphasized in the present trial [17]. Its mechanism was tested in a novel context and at relatively low costs per participant (sum of incentives per employer (€1050)/average cluster size (111/13 = 9) = €124). Grounded in psychological theory and building on previous successful applications, the results encourage further testing.

We suggest three routes for further exploration. First, to test its potential with larger samples. This also allows for more subgroup analyses and effect modification. Second, to test its feasibility in supporting hybrid workplace support programs in the field. Workplace group cessation training is effective and can also be offered online, but the increase in hybrid remote work might limit some of the infrastructural benefits of the workplace. For example, less participants are at the workplace at the same day, as hybrid working has increased flexibility in working hours. The design of interventions for health and safety in a more flexible workplace context is a new public health challenge. In addition, future studies could allow the participation of relatives or peers of employees who do not have active employment. Third, the lotteries can be part of initiatives where participants can choose parts of their incentive; so called tailored designs. Use of these self-incentives alongside behavioral support and cessation medication was shown to be feasible and can be delivered at low-cost [37]. Increased possibilities of e-health can facilitate personalized cessation support, including the design features of incentives [38, 39].

Strengths and limitations

The current trial is subject to some limitations, which have been discussed before [4]. Our sample included mostly higher educated and fewer participants with lower incomes. Smoking is responsible for approximately one third of differences in socioeconomic differences in mortality [40]. From a public health equity perspective, interventions should at the very least have potential amongst people in lower socioeconomic circumstances. We focused in our recruitment on organizations that were likely to employ such populations. In addition, our results are corrected for income and education level. Nonetheless, our final sample was overrepresented by higher educated employees and therefore limited moderation analyses. Follow-up research could set clearer targets for inclusion, allowing for more sub-group analyses. Another limitations is the absence of cigarette use as covariate. We planned to control for pack-years in our analyses. We did assess pack-years to determine trial eligibility via the enrollment system of the training company. While we were able to use pack-years in the automated message informing people whether they were eligible or not, unfortunately the underlying data was not stored and transferred to our systems.

A point of attention in future trials should be to have a clear strategy to minimize the difference between the self-reported and validated abstinence rates. In the present trial, we especially notice this in the control arm. A part can be explained by the higher loss to follow-up rates. Another explanation could be that in the intervention arm, participants replied more often to the biochemical validation request from a sense of reciprocity. At week 52, by design we kept all participation-incentives identical (i.e. 30 euro regardless of smoking status), yet, this did not entirely prevent higher validation rates in the intervention arm.

The COVID-19 pandemic was unprecedented and came with several unforeseen methodological caveats that we care to elaborate on. First, recruitment difficulties at the organizational and participant level. Organizations often stated that the many changes (such as hybrid work, sick leaves, lock-downs etc.) that came with COVID-19 limited their capacities for additional interventions. Studies show that employees could have been coping with job insecurity, and therefore less organizational identification. This might have resulted in a lower willingness to engage in organizational citizenship behavior and commitment to longer-term company initiatives [41]. A second methodological difficulty was an increased uncertainty about the planning of the training due to lockdowns. For instance, several clusters had their first training rescheduled to an unknown date in the future. Although these participants remained in the trial and did start their training later, these groups had a lower proportion of survey responses at baseline and higher loss to follow-up, which is reflected in the relatively high proportion of missing survey responses, especially in the control arm. An adjacent third challenge was to reinvent an effective strategy for attrition. Engagement with participants in uncertain times and fully at distance was challenging. While we were able to accommodate for missing values from the surveys statistically, loss to follow-up limited the potential for the study of tertiary explorations and pathways of effects. Despite the difficulties, COVID-19 also resulted in innovative ways of communicating that are more common or almost standard now (e.g., fully digital communication) and that we can benefit from in future workplace programs.

Another limitation concerned the biochemical verification of self-reports. The primary outcome depended on participants’ willingness to measure and submit their CO-values after the training period had ended. We sought to achieve this by providing a time window (c.f., the RS), applying our retention strategy, and sending reminders. While CO-measurements were well established and widely applied, they could not certify abstinence across the full 52 weeks. We assessed continuous abstinence through two instruments at multiple time points and introduced an unannounced measurement, yet it remained possible that a negative CO-measurement reflected only short-term abstinence.

An adjacent limitation was that unsuccessful participants could have manipulated the procedure, for example, by asking a non-smoker in their surroundings to breathe into the device. We also did not record the time of day at which participants conducted their CO measurements. Since carbon monoxide levels can dissipate within approximately eight hours, it is possible that participants may have taken their readings in the morning before smoking, resulting in lower CO values than if the measurement had been taken later in the day.

We sought to discourage cheating by first requesting a self-reported smoking status and requiring the CO-measurement the following day, and by emphasizing to participants that both smoking and non-smoking statuses were acceptable for study payment at completion. At the main outcome point, neither study arm provided financial motivation to cheat. By additionally applying supportive and trust-inducing language throughout the trial (e.g., conveying that relapse was never a personal failure), we aimed to mitigate this risk further. Nonetheless, future studies could introduce in-person sample checks to increase confidence in the results.

A key strength of this study is its strong theoretical foundation, building on previous applications of leveraging regret theory, while extending it to a workplace setting. This novel approach provides promising avenues for promoting health behavior in the workplace. Furthermore, the study offers insights into the sustainability of behavior change, as it examined behaviors up to six months after the intervention ended. Additionally, smoking status was biochemically validated by CO measurements, which adds robustness to the assessment of smoking cessation outcomes. This dual focus on theory-driven intervention design and long-term follow-up enhances the understanding of both the short- and long-term impacts of workplace health initiatives.

An adjacent strength of this trial is that the intervention balanced between organizational commitment and expenditures. By requiring organizations to cover training and lottery expenses, the approach fostered employer buy-in while maintaining affordability, with total lottery costs equating to only 0.6% of the Dutch minimum weekly wage. Additionally, the training costs were covered by employees’ health insurance, further reducing financial barriers. This increases the chances that the intervention elements are potentially both scalable and adaptable, with the potential for further refinement.

Conclusion

We offered lottery incentives for smoking cessation in the workplace and studied its short-term and long-term effects. We find meaningful and practically relevant results at the main 52-week outcome point, although these results did not reach statistical significance. Three and six months after the quit date, the effect of the regret lotteries did reach statistical significance. Its design was rooted in behavioral economics by using anticipated regret to counteract present biased impulses that lead to immediate gratification and relapse. The results show enough potential to theorize and further apply this method in a field setting, that can benefit from the theoretical, methodological and practical lessons learned in this trial.

Abbreviations

NTR

Dutch trial register

FTND

Fagerström test for nicotine dependence

CO

Carbon monoxide

RS

Russell standard

CI

Confidence interval

SD

Standard deviation

OR

Odds ratio

Ref.

Reference category

p.p.m

Parts per million

COVID-19

Coronavirus disease 2019

Authors’ contributions

KS, ER, NV, MH were responsible for the data collection and trial management. KS and MS were responsible for data analysis. KS & ER wrote the main manuscript. KS, ML, KP and MZ are topic experts and/or grant applicators. All authors read and approved the final manuscript.

Funding

This study was funded by the Strategic Program Sustainable Health and Prevention & Perception and Behavior of the National Institute for Public Health and the Environment (RIVM). The funding body had no role in the design of the study, collection, analysis, and interpretation of data, or writing the manuscript.

Data availability

The datasets generated and analyzed during the current study are not publicly available due to European privacy laws (European General Data Protection Regulation (GDPR)) and according to ethical considerations. The data is stored in accordance with the RIVM-data management policy and is subjected to periodic scientific audits. Data are available upon reasonable request.

Declarations

Ethics approval and consent to participate

All procedures performed in studies involving human participants were in accordance with the ethical standards of the institutional and national research committee and with the 1964 Helsinki declaration and its later amendments or comparable ethical standards. The trial protocol and materials were reviewed and approved by the Radboud University Ethical Review Board (ECSW-2019–114). Informed consent for participation was obtained from all individual participants included in the study.

Consent for publication

Not applicable.

Competing interests

The authors declare no competing interests.