Nicotine preloading for smoking cessation: the Preloading RCT

Intervention group

In the intervention group, participants wore a 21-mg nicotine patch daily for an intended 4 weeks prior to quit day. The intention was that this would be worn for 24 hours per day. However, any participants who had experienced previous AEs at night from 24-hour patch use were advised to wear the patch during waking hours only.

We asked participants to smoke as normal and not reduce nicotine consumption. Reducing consumption would probably lower the nicotine concentration in the blood, which could have resulted in cigarettes being more rewarding and, thus, have undermined the supposed benefits of preloading. 27

We referred patients to the NHS Stop Smoking Service to set a quit day, obtain behavioural support and receive a prescription of pharmacotherapy to support cessation. Although we aimed for this quit day to be 4 weeks from the start of preloading, in keeping with the pragmatic design, we asked participants and NHS clinics to set this date within a window from 3 to 5 weeks after starting preloading. Preloading was allowed to continue for up to 8 weeks in exceptional circumstances. Preloading was also allowed to restart once, if necessary, for example if this was interrupted because a participant was admitted to hospital. In such cases, participants aimed to complete 3–5 weeks of preloading from the date of recommencement. We dispensed NRT in two lots, one of 2 weeks and a second, 1 week later, of 3 weeks. We made arrangements to dispense additional lots of NRT if preloading was extended.

The researchers explained the rationale of preloading and prompted action planning to maximise adherence to the patches, that is, they talked through participants’ daily routine and assisted them to use it and environmental cues to minimise the chance of forgetting to use the patches. They provided reassurance about concerns that participants may have about side effects and how to manage them. A booklet containing this information was supplied to participants. We aimed to see participants 1 week after commencing preloading. At this visit, we asked participants about their experiences and their understanding of the necessity of preloading and again addressed these beliefs as well as concerns about preloading.

We offered participants lower-strength patches from the beginning if they reported experiencing adverse reactions to the 21-mg patch or if, during the treatment course, they experienced symptoms of nicotine overdose such as nausea, salivation and/or pounding heartbeat or other symptoms that they believed were due to the patch strength. We stopped preloading if a participant requested it, if it was not possible to alleviate AEs by reducing the dose or if an intervening health state or contraindication to preloading emerged.

Control group

The research team were keen to offer participants in the control group a placebo, but the NIHR Health Technology Assessment (HTA) Board would not allow this. We were concerned that offering no treatment would lead to disengagement and, to counteract this, we developed a behavioural intervention that could seem plausible to participants but had no evidence that it would increase abstinence. We asked participants to consider their smoking pattern and the triggers for particular cigarettes (e.g. the first cigarette of the day, the first after dinner) and to plan ways to reduce these cues. Such a process is standard in smoking cessation support, so participants in the intervention group were likely to engage in this after preloading and in preparation for quitting. The control group received a booklet outlining this process, which was designed to be comparable to the booklet supplied to the intervention group. As in the intervention group, participants in the control group were referred to the NHS Stop Smoking Service to commence a quit attempt between 3 and 5 weeks after enrolment.

Standard smoking cessation treatment common to both arms

In both arms, at the first and second contacts, we facilitated contact between participants and the local NHS Stop Smoking Service and wrote a referral letter to encourage the NHS Stop Smoking Service to work with us on encouraging participants to continue preloading. In particular, we asked the NHS Stop Smoking Service advisors to ignore the presence or absence of preloading when discussing and recommending the use of pharmacotherapy to support the quit attempt. We especially asked advisors to feel free to use varenicline, which starts prior to quit day and, hence, would be used concurrently with nicotine preloading. This is because we were keen that the treatment provided by the NHS Stop Smoking Services did not differ between trial arms. NICE guidance has specifically recommended against this combination of NRT and varenicline,28 which advisors wrongly assumed was because of safety concerns about concurrent use. We therefore addressed this in the referral letter, by telephone and in face-to-face discussions with the NHS Stop Smoking Service.

The NHS trains Stop Smoking Service advisors to give weekly behavioural support starting 1–2 weeks prior to quit day and continuing until at least 4 weeks after quit day. This support addresses issues such as planning for the quit day, the ‘not a puff’ rule and how to deal with difficult situations, such as others smoking around the person who has quit. It also provides monitoring of behaviour and validation of abstinence through CO testing. The support is largely withdrawal-orientated therapy. 29

Our protocol26 allowed all other medication to be used concurrently with preloading.

Primary outcome

The primary outcome was 6-month prolonged abstinence, defined according to the Russell Standard criteria. 30 This allows a grace period of 2 weeks following quit day when lapses do not count against abstinence. Thereafter, we counted a person as abstinent if they smoked fewer than five cigarettes or cigars up to the 6-month assessment and were biochemically confirmed abstinent by an exhaled CO concentration of < 10 parts per million (p.p.m.).

Secondary outcomes

The secondary outcomes were 12-month Russell Standard abstinence and biochemically confirmed 7-day point prevalence abstinence at 4 weeks, 6 months and 12 months.

Adverse events

We defined AEs as those that occurred after baseline and until 1 week after quit day, thereby covering the period of preloading and an additional week for AEs to emerge. This excluded planned events, such as scheduled surgery. In the protocol,26 we deemed that we would report only AEs of moderate severity or above, that is, those events that hindered or prevented the person going about their normal activities. This is because these events matter more to patients and because NRT has been used for many years and so many common minor AEs are known already.

We assessed the AEs arising from preloading in two ways. First, we elicited AEs from participants in both arms at the contacts at –3 weeks (1 week after baseline) and +1 week (5 weeks after baseline and 1 week after quit day). Spontaneously occurring AEs were coded at the level of preferred term and system organ class using the MedDRA (Medical Dictionary for Regulatory Activities) coding system. 31 However, spontaneously occurring reports may introduce bias. It seemed illogical to participants in the control group and to treating staff to discuss AEs when the participant was taking no medication at all. Therefore, second, at 1 week after baseline we also gave all participants a questionnaire concerning symptoms of nicotine overdose in the previous 24 hours (such as nausea and excessive salivation).

We defined serious adverse events (SAEs) as those leading to hospitalisation, death, permanent disability or congenital abnormality and reported these separately. We obtained the medical history of participants experiencing SAEs and these were classified by an independent assessment panel blinded to allocation as unrelated or unlikely to be, possibly, probably or definitely related to the use of nicotine patches.

Effect modification

This chapter addresses two questions. The first examines effect modification or moderation of the possible treatment effect of preloading. It is possible that preloading was effective only for a subgroup of the population of smokers seeking help to quit. Given its proposed mechanism of action on undermining the reward from smoking and the drive to smoke, we hypothesised that preloading would be more effective for people who showed evidence of higher dependence on cigarettes. This might be evidenced by a higher cigarette consumption at baseline (shown by cigarettes per day or exhaled CO concentration at baseline) or a higher dependence score (FTCD). Understanding this may help us target preloading to the group who stand to gain a greater than average benefit from preloading, thereby maximising the cost-effectiveness of the treatment approach.

Mechanism of action of preloading

The second question addresses the question of how preloading may work.

As discussed in Chapter 1, Mechanisms of action of preloading, our review of the mechanisms of action of preloading revealed scant evidence for any of these mechanisms explaining the possible effectiveness of this strategy. This is important for clinical practice. Nicotine preloading may not help everyone who is trying to stop smoking. Therapists could monitor whether or not preloading is achieving its intermediate effects and, if not, abandon the strategy early, saving resources on behalf of the NHS. In this chapter, we examine the possible mediating pathways between nicotine preloading and outcomes.

Design

The trial protocol and main outcomes are described in Chapters 2 and 3. For the moderation analysis, we followed the same analysis strategy as outlined in Chapter 2, Statistical analysis, but added multiplicative interaction terms to the equation between two markers of dependence assessed at baseline and trial group. As markers of dependence we used FTCD, the standard measure of baseline dependence, and exhaled CO concentration. The latter is a measure of smoke intake in the preceding hours; more dependent smokers draw more heavily on their cigarettes or smoke more cigarettes per day and, hence, tend to have higher CO measurements.

For the mediation analysis, we followed the regression framework described by Kenny. 41 The steps are as follows:

1. show that the preloading variable causes smoking cessation (Chapter 3)

2. show that preloading causes change in the mediator

3. show that change in the mediator is associated with smoking cessation

4. to establish complete mediation, show that controlling for change in the mediator abolishes the association between preloading and cessation.

Given that Chapter 3 showed that, on adjustment for the effect of post-cessation varenicline, there was evidence for the efficacy of preloading, this chapter deals with steps 2–4.

Outcomes

For the moderation analyses, the outcome was the primary outcome: Russell Standard 6-month abstinence.

We assessed the impact of preloading on potential mediators of effect outlined in Figure 5. These were measured 1 week after starting preloading or the control condition (3 weeks prior to quit day) and were:

• positive reinforcement – modified Cigarette Evaluation Questionnaire (mCEQ) satisfaction subscale42 and noticing whether cigarettes were more or less enjoyable than previously

• negative reinforcement – mCEQ reward subscale

• drive to smoke – self-reported change in urge strength and change in frequency of the urge to smoke combined, assessed using the Mood and Physical Symptoms Scale – Craving (MPSS-C) subscale;43 smoking stereotypy taken from the Nicotine Dependence Syndrome Scale;44 the mCEQ craving question; and a question used by Hajek et al. 21 in a similar trial that asked participants to rate their urge to smoke compared with usual

• cigarette consumption – cigarettes per day and exhaled CO concentration

• symptoms of addiction – modified score on the FTCD,45 modified by removing cigarette consumption from the scale to ensure that symptoms of addiction were distinct from cigarette consumption.

FIGURE 5.

Effect of preloading compared with control on the primary outcome, depending on baseline tobacco dependence. (a) FTCD score (0–3, 4–6 and 7–10); and (b) baseline exhaled CO concentration in p.p.m.

The hypothesis is that, by undermining the learned addiction to cigarettes during the pre-quitting period, preloading reduces the intensity of craving and withdrawal during the post-quit period. For this, we examined the effect of preloading on the intensity of urges and mood symptoms at the end of the first week of abstinence. We used the MPSS-C and the Mood and Physical Symptoms Scale – Mood (MPSS-M) subscales to measure these. The results of assessments of craving and withdrawal symptoms in those who are smoking can be hard to interpret,46 so we analysed these once in those who had been perfectly abstinent and once in those who were continuing to try to be abstinent.

For our other three mediational hypotheses, we assessed the impact of the possible mediators measured at 1 week after commencement. These were as follows:

1. Medication adherence: days of use of post-quit day medication measured at the +1-week visit.

2. Confidence question: ‘How high would you rate your chances of giving up smoking for good at this attempt?’, measured on a five-point scale (with 1 being ‘not at all’ and 5 being ‘extremely good’).

3. Nausea and aversion: we assessed nausea using the mean scores for two questions derived from themes from participant interviews in a previous trial. 47 These were ‘Over the past week how nauseous have you felt when you have seen cigarettes or lighters?’ and ‘Over the past week how nauseous have you felt when you have smelt cigarette smoke?’ and were measured on five-point scales from not at all to extremely. Aversion was measured using the aversion subscale of the mCEQ.

To maximise the sensitivity to detect mediation in the mediator analyses, our outcomes were Russell Standard 4-week and 6-month abstinence. Given that 4-week abstinence is more proximate to the mediators, it should have a stronger association with the mediators than 6-month abstinence.

Statistical analysis

The moderator analysis used the same model as for the primary analysis outlined in Chapter 2, Statistical analysis, but added, in turn, our two markers of dependence (FTCD and exhaled CO concentration) and the multiplicative term representing the baseline marker of dependence multiplied by the trial group indicator variable.

In all of the mediator analyses, we excluded people who had missing data on the mediator. In the analyses, we examined for evidence of mediation on variables assessed at –3 weeks (1 week after baseline) and at +1 week (5 weeks after baseline, 1 week after quit day).

For the second step of the mediation analysis, we assessed the effect of treatment group on mediators descriptively by comparing means between treatment groups and then by analysis of covariance, with adjustment for centre and for the baseline value of the mediator when applicable; thus, effectively examining the effect of preloading on change in the mediator. We checked the residuals to ensure that there was no marked deviation from normality.

We proceeded to the third step of mediation analysis only for those variables for which there was reasonable statistical evidence that preloading influenced the change in the mediator. We assessed the effect of mediators on abstinence outcomes at 4 weeks and 6 months using logistic regression. We looked at this first in unadjusted analysis and then with adjustment for treatment group, as advocated for mediation analysis by Kenny. 41 As previously, these analyses were adjusted for stratification by centre.

In the fourth step of mediation, we examined whether or not potential mediators (i.e. those correlated with both the treatment group and the outcome) did indeed mediate the relationship between treatment group and each outcome; this was done by adding each to a logistic regression model including the mediator and the treatment group. Given that there was strong statistical evidence for the efficacy of preloading only when adjusted for use of varenicline, we used the model adjusted for varenicline as the primary model in this analysis. We added each potential mediator singly and then all of the mediators in the same model.

Modification of the effect of preloading on abstinence by baseline tobacco dependence

There was no evidence that people who were more dependent on smoking received a greater benefit from preloading. The p-values for multiplicative interaction terms for the effect of preloading in those with higher dependence scores and a higher exhaled CO concentration were 0.831 and 0.171, respectively. Per unit increase in each variable, the ORs were 1.01 (95% CI 0.90 to 1.14) and 1.01 (95% CI 0.99 to 1.04), respectively (see Figure 5).

Effect of preloading on potential mediators

Effect of preloading on the outcome, controlled for mediators

In the final step of the mediation analysis, we considered whether or not the strength of association between use of preloading and abstinence was diminished after adding three potential mediators. These mediators, all of which showed evidence of potential mediation in the previous steps, were (1) noticing that urges were weaker than usual while still smoking, (2) reduced exhaled CO concentration while still smoking and (3) reduced urge strength after abstinence. As the clear evidence of efficacy of preloading emerged only in the analyses adjusting for post-cessation varenicline use, we used this as the primary comparison for this final stage of mediation analysis. In the data on abstinence, we included all participants in the analysis with the presumption that people who dropped out were smoking. However, where people were not followed up, the value of their mediator was not imputed and so these participants were dropped from the analysis. To ensure that the ORs were comparable across analyses, the number with valid data was used on the mediator in all analyses, including those analyses that did not include the mediator.

There was evidence that each of the mediators explained the effect of preloading to some extent (Table 12). Controlling for a reduction in urge strength reduced the effect of preloading on abstinence by 47% for 4-week abstinence and 59% for 6-month abstinence. Controlling for a reduction in exhaled CO concentration during the pre-quit period reduced the effect of preloading on abstinence by 23% for 4-week abstinence and 14% for 6-month abstinence. Controlling for a reduction in craving after quitting reduced the effect of preloading on abstinence by 28% for 4-week abstinence and 21% for 6-month abstinence. Controlling for all three potential mediators reduced the effect of preloading on abstinence by 71% for 4-week abstinence and 78% for 6-month abstinence.

Conclusion

These limited reflections on participants’ feelings about preloading suggest that most participants found it helpful and that the large majority would recommend preloading.

Costs

Total costs comprised the intervention costs, NHS Stop Smoking Services costs, AE costs, health resource use costs and medication costs.

Outcome

The outcome used in the cost-effectiveness analysis was 6-month prolonged Russell Standard abstinence, which was the primary outcome of the trial. The 4-week quit rate and 12-month prolonged abstinence, measured according to the Russell Standard, were also used for the secondary analysis to provide comparison with national statistics. The methods of calculation were the same as for the primary statistical analysis.

Analysis

Costs

Analysis

Sensitivity analyses

To explore the uncertainty surrounding the results, 5000 bootstrap iterations were used to plot the cost-effectiveness plane and CEAC. Figure 6 presents the cost-effectiveness plane, which shows a cluster of ICERs scattering across all four quadrants. Although the overall majority fell to the right side of the zero incremental abstinence rate line, indicating a more effective intervention, over half of those concentrated in the north-east quadrant, indicating a more expensive intervention.

FIGURE 6.

Cost-effectiveness plane of incremental costs and incremental abstinence rate at 6 months post quit date, comparing the preloading group with the control group.

Figure 7 presents the CEAC to illustrate the bootstrapping iterations. The CEAC shows that the probability of preloading being cost-effective, compared with the control group, increased with the increase in costs (i.e. uncertainty of the results reduced). When the costs reached £3600, the probability of preloading being cost-effective was approximately 80%. For the probability to reach 90%, another £3300 would be required. Soon after this point, the curve became flat, stabilising at about 96%.

FIGURE 7.

Cost-effectiveness acceptability curve of the probability of preloading being cost-effective compared with the control group.

Clinical trial

The clinical trial compared treatment with nicotine patches for 4 weeks prior to a planned quit date (intervention) with no pre-treatment prior to a planned quit date (control). Both the intervention and control groups also received standard behavioural counselling prior to the quit date. Biochemically validated 12-month abstinence was achieved by 14.0% of the intervention group and 11.3% of the control group. In the primary analysis, this gave an unadjusted OR of 1.24 (95% CI 0.97 to 1.58; p = 0.086) and a RD of 2.71 (95% CI –0.37 to 5.78; p = 0.085). As expected, there was an imbalance between arms in the frequency of use of varenicline for post-cessation medication; adjustment for this gave an OR of 1.30 (95% CI 1.02 to 1.66; p = 0.036) and a RD of 3.31 (95% CI 0.22 to 6.39; p = 0.036) between the intervention and control groups.

Economic model

A Markov model (EQUIPTMOD), developed as part of EQUIPT, was used to estimate the long-term costs and effects of using NRT pre-treatment compared with no pre-treatment in a hypothetical cohort of smokers with the same age and sex distribution as in the trial, who make a one-time attempt at quitting smoking. EQUIPTMOD allows the determination of the impact of either continuing or stopping smoking on both morbidity and mortality outcomes and costs. In this chapter, we estimate the lifetime costs, QALYs and life-years associated with NRT pre-treatment compared with no pre-treatment.

Design of the model

There are three primary states within the model: (1) current smoker, (2) former smoker and (3) dead (Figure 8).

FIGURE 8.

Model schematic.

With each 1-year cycle, the cohort is subjected to a set of transition probabilities that allow them to either stay within their current state or move to one of the other two states. Death is an absorbing state, meaning that those who enter this state remain within the state. We ran the model until participants reached the age of 100 years or died.

The model is replicated for different population cohorts based on the age and sex distribution of patients within the clinical trial. To obtain trial population-level estimates, these cohort-level estimates are weighted by the percentage of the trial population falling into each age and sex cohort.

To estimate the impact of the intervention on costs and smoking-related outcomes, two separate models were created: one that simulates a cohort of smokers who quit in the first year and one that simulates a cohort of smokers who do not quit in the first year. The results of the two models are combined by weighting the outputs by the trial population and the effectiveness of the intervention and the control.

Transition probabilities

Transition probabilities incorporated within the model include:

• the probability of quitting smoking in the first cycle (year) based on the effectiveness of the intervention and the control within the trial

• the age- and sex-specific annual probability of mortality associated with current smoking and being a former smoker

• the probability of smoking cessation and relapse over the long term in current and former smokers.

The probabilities of smokers successfully quitting in the first year after the intervention were based on the biochemically validated 12-month abstinence rates from the clinical trial. Based on this measure, 14.0% of those in the intervention group and 11.3% of those in the control group were abstinent at 12 months. In the base-case analysis, the 12-month abstinence rate was assumed to be predictive of long-term cessation. This was tested within sensitivity analyses through applying a rate of relapse of 30% in the second year after the intervention. 68 Smokers who did not quit smoking, or who relapsed, were subjected to the same background quit rate in all subsequent years, which is reflective of the balance of quitting and relapsing over a lifetime. 69

The probability of death by age, sex and smoking status was calculated using the attributable risk of death based on smoking status. The following was required for this calculation: age- and sex-specific probabilities of death in the general population; the age- and sex-specific prevalences of smoking status (current, former or never smokers); and the RR of death by smoking status. Mortality rates were based on actuarial life tables and the age- and sex-specific prevalences of smoking were derived from the survey data. 70,71 The RRs of death for former and current smokers compared with never smokers were derived from published data19 (see Appendix 1, Table 29).

Long-term cessation and relapse were modelled through the application of an underlying quit rate, which applies to all age- and sex-specific cohorts after the first year. This was estimated at a value of 2% per annum and represents the balance between those quitting smoking each year and those who start smoking or relapse. 69

Prevalence of smoking-related diseases

The smoking-related population attributable fraction relating to current and former smokers for smoking-related diseases was estimated based on epidemiological data. The model estimates, for each cycle, the prevalence of smoking-related diseases based on the proportion of the cohort who are either current smokers or former smokers.

Four diseases, lung cancer, coronary heart disease (CHD), chronic obstructive pulmonary disease (COPD) and stroke, were found to be responsible for the majority of the smoking-related disease burden and were, therefore, incorporated within the model. 72,73 The number of cases each year of these diseases was derived through calculation of the attributable fraction based on the prevalence of smoking-related diseases in England, the prevalence of smoking status in England (current, former or never smokers) and the relative effect of smoking on the prevalence of each disease49,74–78 (see Appendix 1, Tables 30–36).

Costs

Within the model, costs comprised both the smoking cessation costs of the intervention and control arms of the clinical trial and the health-care costs associated with smoking-related diseases.

Prior to the planned quit date, both the control group and the intervention group received standard behavioural counselling. In addition, those in the intervention group also received 4 weeks of NRT. Based on the within-trial analysis, this resulted in a mean cost per person of £58 [standard error (SE) £0] in the intervention group and £11 (SE £0) in the control group. Furthermore, prior to the quit date, both treatment arms received NHS Stop Smoking Services, with a mean cost per person of £124 (SE £1) in the intervention group and £122 (SE £1) in the control group. The cost of the NHS Stop Smoking Services accessed over the 12 months after the quit date was also included in the analysis: £133 (SE £6) for the intervention group and £103 (SE £5) for the control group, based on the within-trial analysis. This resulted in total costs overall for smoking cessation of £295 (SE £6) for the intervention group and £236 (SE £6) for the control group.

The annual costs for an individual with each of the diseases were estimated based on a systematic literature review. Costs relate to prevalent cases of disease. The annual cost for COPD is £1042.57, for lung cancer is £7002.65, for CHD is £1247.79 and for stroke is £5886.6679–82 (see Appendix 1, Table 36).

All costs were inflated to the year 2016 using the Hospital and Community Health Services Index83 (see Appendix 1, Table 37).

Utility values

Utility decrements associated with smoking-related diseases were derived from the US Medical Expenditure Panel Survey. 84 Utility values based on current smoking status (current or former smoker) were derived from the Health Survey for England adjusted for relevant covariates including disease prevalence. 85 The EuroQol-5 Dimensions, a validated instrument for measuring health-related quality of life, was used for both sets of utility values and UK tariffs were used for calculating utility scores86 (see Appendix 1, Table 38).

Outcomes

The costs, life-years and QALYs associated with both the intervention and the control groups were estimated over the lifetime of the cohort. In the base case, both costs and effects were discounted at a rate of 3.5% per annum as per NICE guidance. 87 A 1.5% per annum discount rate for costs and outcomes was tested in the sensitivity analyses. The analysis was conducted from the perspective of the NHS.

The incremental cost–utility ratio, expressed as the incremental cost per QALY gained, was reported to assess the cost-effectiveness of the intervention group compared with the control group.

Key assumptions

As is the case with all models, a number of assumptions were required to estimate the economic impact of tobacco-control interventions; these have been detailed in a previous publication67 and are summarised in Box 1.

Handling uncertainty

The effect of parameter uncertainty on the calculated outcomes was assessed through probabilistic sensitivity analyses involving Monte Carlo simulation. 88 Standard probability distributions were included for the natural history parameters, RRs and ORs, costs and utilities. Beta distributions were used for transition probabilities and utility values by smoking status, normal distributions were used for utility decrements due to disease, log-normal distributions were used for RRs and ORs and gamma distributions were used for costs. Population-level data were assumed to be fixed. Distribution parameters can be found in Appendix 1, Tables 35–38. The background quit rate was parameterised using a beta distribution. As distributional data were not available we assumed a conservative sample size of 50 for the parameterisation.

A set of 5000 outcome estimates were obtained, with the results displayed using a scatterplot of incremental costs versus QALYs and a CEAC that graphically presents the probability that the intervention is cost-effective as a function of the willingness of decision-makers to pay for an outcome (QALY). 88

Base-case analysis

The total lifetime costs within the intervention group were £13,111 and within the control group were £13,177 (a difference of £66). The costs associated with smoking cessation, which included both behavioural and pharmacological interventions, were higher in the intervention group (£295) than in the control group (£236; a difference of £59). Health-care costs associated with smoking-related diseases over a lifetime, however, were lower in the intervention group (£12,816) than in the control group (£12,941; a difference of £125) (Table 26).

A greater number of individuals quit smoking in the intervention group than in the control group (139 per 1000 smokers vs. 112 per 1000 smokers, a difference of 27 individuals). The greater number of individuals quitting smoking in the intervention group resulted in more discounted life-years lived in the intervention group than in the control group (17.977 life-years vs. 17.957 life-years) and more QALYs (14.300 vs. 14.267). The intervention is dominant over the control as the intervention was both more effective, producing both more QALYs and more life-years, and less costly.

Additional analysis

An analysis was conducted adjusting for an imbalance in the use of varenicline post quit date within the two groups (Table 27). The adjusted RD for cessation at 12 months was 3.31 (95% CI 0.22 to 6.39), compared with a RD of 2.71 (95% CI –0.37 to 5.78) for the base case. The adjusted difference in smoking cessation costs was £63 (95% CI £52 to £78), compared with £59 (95% CI £44 to £74) in the base case.

After adjustment for varenicline imbalance, there were 33 more people who quit in the intervention group than in the control group; this is six more people who quit than in the unadjusted analysis. The difference in total costs was also greater, with the intervention costs being £90 lower than the control costs. The intervention also resulted in more QALYs (a difference of 0.040) and life-years (a difference of 0.025) than the control. As in the base-case analysis, the intervention is dominant over the control as it is both less costly and more effective.

Deterministic sensitivity analysis

The cost-effectiveness results were robust to an alternative discount rate of 1.5% per annum for costs and outcomes, with the intervention remaining cost saving (£19,273 for the intervention group vs. £19,384 for the control group) and resulting in more QALYs (19.091 for the intervention group vs. 19.043 for the control group) (Table 28).

With a relapse rate of 30% after the first year, the cost difference between the intervention group and the control group was reduced, as were the QALY and life-year differences. However, the intervention remained less costly and more effective than the control and is, therefore, still dominant over the control (Table 28).

Probabilistic sensitivity analysis

As can be seen from the scatterplot of incremental costs compared with incremental QALYs (Figure 9), the majority of the estimates (80%) are within the lower right quadrant, indicating that the intervention is dominant over the control. As is evident from the CEAC (Figure 10), at a willingness-to-pay (WTP) threshold of £20,000 per QALY there is a 94% probability that the intervention is cost-effective. There is a 95% probability that the intervention is cost-effective at a WTP threshold of £30,000 per QALY.

FIGURE 9.

Scatterplot of incremental costs vs. incremental QALYs for the intervention group vs. the control group.

FIGURE 10.

Cost-effectiveness acceptability curve for the probability that the intervention is cost-effective with a relapse rate of 0% after year 1.

If 30% of smokers who quit in the first year are assumed to relapse, there is a 93% probability that the intervention is cost-effective at a WTP threshold of £20,000 per QALY and a 94% probability that the intervention is cost-effective at a WTP threshold of £30,000 per QALY (Figure 11).

FIGURE 11.

Cost-effectiveness acceptability curve for the probability that the intervention is cost-effective with a relapse rate of 30% after year 1.

Summary of main findings

In this pragmatic open-label trial testing the effect of nicotine preloading for 4 weeks prior to a quit day, there was no evidence that preloading increased the proportion of people achieving smoking abstinence. Adherence to the nicotine patch used for preloading was good, with the large majority using treatment as prescribed. Preloading was tested in a clinical setting where smokers could opt to use either NRT or non-nicotine pharmacotherapies for continued cessation treatment after preloading had ended. Preloading encouraged the use of NRT for cessation treatment or deterred the use of varenicline as post-quit day medication. Varenicline is more effective than other medications, so in a planned analysis we adjusted for its use after quit day. This led to clear evidence that preloading itself did increase the likelihood of achieving abstinence. There was no evidence that use of varenicline undermined the effect of preloading. Most people continued with the preloading treatment, implying that it is well tolerated. Around 1 in 20 people suffered AEs of moderate severity and above as a consequence of the treatment, principally nausea. There was no evidence of an excess of SAEs.

Public involvement

The study was run under the auspices of the UK Centre for Tobacco and Alcohol Studies (UKCTAS). 89 UKCTAS has a standing panel of public members who guide the research programme, helping select topics that matter to people who smoke and shaping the way that research is carried out. Before the study started, we discussed the study and the methods with the panel. One member of the panel joined the trial steering committee that provided oversight to the trial.

In the early days of the study, we encountered a much slower rate of recruitment than we had anticipated. We used the method of recruitment that we had employed in three of the four centres in previous trials. 17,32,36 In the past, around 5–10% of people who received an invitation letter from their GP had enrolled in our studies. As in this trial, in the previous trials the invitation letter invited people wanting to stop smoking to seek support, rather than emphasising the novel treatment. We know from discussions with previous participants that it is the opportunity to receive support to quit that is the main draw for potential participants. In the Preloading trial, only around 1% of people who were invited enrolled in the trial. We asked GPs to write to batches of participants, 100 at a time, to ensure that we had a reasonable number of initial appointments to fill the clinic but did not generate a waiting list. However, initial recruitment was much slower than anticipated and, therefore, accrual into the study was much slower than planned.

As a consequence, we consulted with eight members of the UKCTAS panel to review our recruitment material and two other members of the public from the Clinical Research Network. They commented on the documents and answered questions about our material. Our recruitment material in the Preloading trial, as in previous trials, was very brief, which is probably important in attracting people who smoke. Consequently, only a few minor amendments were suggested, which we implemented after approval from the ethics committee. However, the response to the recruitment letter remained as poor as it had been. In fact, the Preloading trial coincided with a downturn in interest in NHS Stop Smoking Services and a rise in the use of e-cigarettes; it is thought that these two factors may be linked. We enhanced our recruitment rate by sending more letters per practice in larger batches and using Docmail^® (CFH Docmail Ltd, Radstock, UK) to send the invitations, easing the burden on general practices. We also added other means of recruitment including text messages from practices and advertising.

At the time of writing, the results of this trial have only just become available. We plan to return to the UKCTAS panel with the results and discuss them with the members. To help guide implementation into policy and practice, it will be important to obtain the public’s views on what the results mean and what would make a person who wants to stop smoking take up preloading.

Strengths and limitations

This trial has several strengths. The trial had power to detect the modest benefits that may have been expected, given the previous meta-analyses. 12 It was conducted with rigour, with a prespecified protocol and analysis plan; it followed standards set out in CONSORT (Consolidated Standards of Reporting Trials) guidelines90 and achieved high follow-up rates compared with many trials of smoking cessation interventions, increasing confidence in the findings. It is the first trial of preloading to assess AEs to standards set out in Good Clinical Practice. In an open-label trial such as this, it is non-intuitive, both to participants and to trial staff, to report and enquire about AEs occurring in people on no medication. We trained our staff to enquire in the same way regardless of trial group, but it remains possible that the open-label design may have led to over-reporting of AEs in the preloading group. By also actively soliciting reports of likely AEs by questionnaire in all participants, we may have removed some of this bias. However, both methods revealed a somewhat similar profile, with nausea being the most common adverse consequence of preloading specifically. Patients also reported other well-established AEs of using a nicotine patch relating to its stimulant (poor sleep and dreaming) and adhesive (skin irritation) properties, but these were uncommon. However, taken together, both methods showed that severe AEs are rare and that the medication is well tolerated. A further strength of the study is that we collected data on potential mechanisms of action of preloading; these are addressed in Chapter 4.

The open-label design could be viewed as a limitation. Most notably, the open-label design led to 29.5% of participants in the control group choosing to use varenicline for post-quit day medication compared with 22.1% in the preloading group. This is a modest absolute difference, but, in this study, use of varenicline more than doubled the odds of achieving the primary outcome compared with the use of an alternative pharmacotherapy (chiefly NRT) and, in our pre-stated analysis, adjustment for this difference led to a statistically significant effect of preloading on the primary and secondary outcomes. There were also more people in the preloading group who used nicotine patches only, possibly because they received 5 weeks’ supply of the medication. The two study arms also had different expectations, which may have affected their smoking behaviour and their responses to various subjective ratings meant to assess the effects of preloading on smoking reward, enjoyment and urges to smoke. A blinded design would probably have shown more clearly an effect of preloading on smoking abstinence and would allow an unbiased analysis of mediators.

The open-label design could be seen as a strength because it produced an outcome that would not have been detected in a blinded design. If patch preloading reduces the use of varenicline, this would suggest that, within the NHS Stop Smoking Services, preloading is an efficacious strategy, but not an effective one, because preloading would be used in an open-label manner in that context. It is unclear, however, whether the difference in varenicline use arose because patients who were happy on NRT opted to continue it or because smoking cessation therapists or prescribers (mainly GPs) were unhappy to prescribe varenicline to someone already using NRT. We sought to counter the latter effect in discussions and with a letter of referral from the research team to the NHS Stop Smoking Services, which took on the pre- and post-quit support and prescribing. However, we know of several instances where prescribers could not be persuaded that co-prescribing the medications was safe, as NICE guidance was viewed as ‘trumping’ this. Revised NICE guidance could easily remove the apparent prohibition on concurrent use. If the difference was due to patients feeling content with patches and disinclined to add another medication, informing patients that adding varenicline improves outcomes would be another potential remedy.

Thus, the open-label design may be viewed as a weakness because it clouded the answer to the scientific question of efficacy and mechanisms of action of preloading, and as a strength because it revealed the effect of preloading as it would play out in the current UK NHS or similar health systems. That said, it is likely that we would be able to overcome the effect on use of varenicline subsequently through changes to guidelines and discussion with patients.

Comparison with other literature

Our previous meta-analysis yielded a RR of 1.16 (95% CI 0.97 to 1.38) for prolonged abstinence, but a RR of 1.26 (95% CI 1.03 to 1.55) for nicotine patches. 12 In this trial, the RR for the primary outcome (also prolonged abstinence) was very similar, at 1.27 (95% CI 1.03 to 1.57), in the analysis adjusted for the use of varenicline. The previous meta-analysis of nicotine patches alone was from an exploratory subgroup analysis and the main analysis showed no evidence of effectiveness, with a RR of 1.16 (95% CI 0.97 to 1.38). Thus, compared with the current literature, the trial has strengthened the evidence for the efficacy of preloading. However, our trial is the only trial to be carried out in a context in which the therapists who prescribed the preloading (our trial team) were different from those who prescribed the post-cessation support (the NHS Stop Smoking Service). Arguably, the context of this trial is more likely to reflect that of most health systems, where there is less behavioural support and dedicated smoking cessation expertise available to people who want to stop smoking than has been the case in the previous efficacy trials, thus revealing an effect that could negatively affect the impact of preloading.

One other factor also deserves attention. In this trial, we asked centres to record the proportion of people who did not make a quit attempt. We were concerned that deferring a quit attempt may mean that a person loses motivation to make one, thereby undermining the effect of preloading. This variable was incompletely recorded by centres, and it was clear that practice with respect to recording also differed in a way that makes relying on this variable unwise. From cross-tabulating other relevant data recorded, it appears that 112 (6.3%) people did not make a quit attempt: 60 (6.7%) of these were in the preloading group and 52 (5.8%) were in the control group. As the proportion was similar in both arms, this is not an effect of preloading per se, but it could reflect the fact that participants waited 4 weeks to quit smoking and we know that plans to quit smoking change quickly. 91 Not many smoking-related trials record the proportion of participants who do not make attempts to quit smoking. However, some of our previous trials have recruited in largely similar ways to this trial and, in these trials, 3% and 12% made no attempt to quit smoking, with a much shorter delay (1–2 weeks and 1 day) between trial enrolment and the target quit day. 33,36 A more recent trial reported that 17% of people who had undertaken 2 weeks of preloading failed to make a quit attempt, but this was defined as not achieving 24 hours of abstinence after quit day. 17 Evidence suggests that around half of all quit attempts do not achieve this milestone, meaning that perhaps only 8–9% failed to make a quit attempt. 92 Taken with these other trials, it appears that preloading and the necessary delay in making a quit attempt is not deterring people from following through with that attempt.

Interpretation

This trial has clarified the role of preloading in the treatment of tobacco dependence. Preloading is an efficacious strategy that could lead to around 3% of people who are seeking help to quit smoking achieving 12-month prolonged abstinence, who might not otherwise have done so. This effect may seem small, but the current 12-month abstinence rate in the UK specialist Stop Smoking Services is 8%93 and so an additional 3% would represent a worthwhile improvement. A failed quit attempt is likely to cost a person about 3–5 years of life expectancy. 34 Thus, around 12 people need to use preloading to gain around 1 year of life. However, within the specific setting of the NHS Stop Smoking Services, without changing NICE guidelines and informing advisors, the efficacy of preloading could be undermined by the effect it has on deterring use of the most effective cessation medication (varenicline) and, possibly, by delaying quit attempts in those motivated to quit immediately. Thus, it seems sensible to confine it as a strategy for use in highly controlled circumstances. If used in NHS Stop Smoking Services, we would recommend that NHS advisors discuss the choice of post-cessation treatment at the start of any period of preloading so that experience of preloading does not deter the use of varenicline.

Our study is not the only study that has produced observational evidence of the superiority of varenicline in routine NHS practice. The recent HTA-funded ELONS (Evaluating Long-term Outcomes of NHS Stop Smoking Services) study showed that the OR for use of varenicline compared with non-use of varenicline was 1.7 (95% CI 1.3 to 2.3),93 very similar to the OR of 2.2 in this study. A Cochrane network meta-analysis of trials gave an OR of 1.57 (95% credible interval 1.29 to 1.91) for varenicline compared with single-form NRT and an OR of 1.59 (95% credible interval 1.29 to 1.96) for varenicline compared with bupropion. 6 A subsequent very large trial produced ORs of 1.68 (95% CI 1.46 to 1.93) for varenicline compared with the NRT patch and 1.75 (95% CI 1.52 to 2.01) for varenicline compared with bupropion. 94 The randomised trials suggest that the superiority of varenicline in these observational data is probably because varenicline is more effective both within and outside the context of a clinical trial. This suggests that a way to improve the outcome of the NHS Stop Smoking Services is to increase the proportion of patients who use varenicline. The ORs of 1.7 and 2.2 for use of varenicline compared with non-use of varenicline compare favourably with those for preloading (1.25 for the primary analysis and 1.34 for the varenicline-adjusted analysis); the use of varenicline seems simpler, and requires less service change, than implementing a new strategy of preloading.

It is important to note that these conclusions relate to preloading as we implemented it in this trial. It remains possible that preloading performed in other ways or in contexts other than the UK NHS Stop Smoking Services, which provide a range of medications and behaviour support free of charge, may improve outcomes to a greater extent. We used a 4-week period of preloading, which, theoretically, ought to be more effective than the 2 weeks used in several previous studies. However, there is no clear evidence that this is so; therefore, limiting preloading to a shorter period could overcome the possible disadvantages that significantly delaying a quit attempt may entail. Theoretically, it is also possible that higher doses of nicotine could lead to greater effectiveness. 95 The additional 21 mg of nicotine per 24 hours preceding quit day was generally well tolerated and other research shows that 63 mg of nicotine per day appears to be well tolerated too. 91 In addition, the higher-dose NRT reduced consumption to a greater extent than the 21-mg patch that was used, suggesting that higher doses may be effective.

It is also possible that varenicline preloading may be effective. One small trial showed that varenicline preloading more than doubled the number achieving 12-week abstinence. 21 A further trial produced somewhat less positive results, but the trial was too small to offer a precise estimate of effect. 96 Consequently, there is no evidence that varenicline preloading improves long-term abstinence, but, given that the RR of achieving abstinence through use of a smoking cessation medication appears to be constant, whether measured early or late in a quit attempt,97 we might expect that it does. Thus, future trials of preloading might want to examine whether or not this promising effect of varenicline holds in a larger trial and manifests in an increased proportion of participants achieving long-term abstinence.

Summary of findings

There was no evidence that preloading was more effective for those showing a greater dependence on smoking. Participants allocated to preloading compared with the control condition showed a reduced reward from smoking, a reduced urge to smoke and reduced smoke inhalation prior to quitting and lowered their cigarette consumption. After attempting abstinence, participants using preloading experienced a reduced craving for cigarettes. Of these possible mediators, only a reduced urge to smoke before and after quit day and reduced consumption while using preloading were associated with abstinence. Together, these changes appeared to mediate most of the effect of preloading on abstinence. Although preloading increased feelings of aversion to smoking, these feelings were not associated with an increased likelihood of achieving abstinence and, thus, there is no evidence that this was an important mediating mechanism. There is also no evidence that the effect of preloading on abstinence was explained by increased confidence in quitting or increased adherence to post-cessation medication.

Strengths and limitations

This study has several strengths. Chief among these are that we planned a comprehensive evaluation of the mechanism of action, assessing all steps in the pathway, and we included analyses of competing hypotheses that were advanced to explain the preloading effect. Being the largest trial to date and the trial with the most comprehensive data on mediators means that the pathway of effect has been clarified. The trial also has some limitations. Our follow-up of participants to assess the effect of preloading on mediators while smoking was carried out only 1 week after commencing treatment. This follow-up was timed to maximise adherence to preloading and to allow the dose to be adjusted if needed. However, previous trials have suggested that the effect of preloading on smoking increases with duration;21,96 therefore, we may have seen larger associations between preloading and change in mediators and between change in mediators and abstinence if this assessment had taken place later. Another issue is that our analysis does not account for the multistep nature of mediation. Our hypothesis was that preloading reduces the strength of urges to smoke while in the pre-quit phase and these reduced urges reduce cigarette consumption. However, we modelled these mediators as separate ‘parallel’ mediators rather than in a structural equation model. Finally, the open-label trial leaves open the possibility that some of these effects are subject to bias, such as participant expectations. Participants in the intervention group were told about the proposed mechanism of preloading to motivate them to adhere to the medication. Thus, the effect of preloading on the proposed mediators could at least partly be caused by this effect rather than by the pharmacological action of the additional nicotine. However, we might have seen an increase in confidence in the preloading group if this was driven by expectations of a positive outcome and this was not apparent. It, therefore, seems less likely that participants’ expectations could explain the increase in abstinence and, therefore, this may be an unlikely explanation of the apparent mediation.

Comparison with other studies

Our analysis of whether or not the effect of preloading depends on baseline tobacco dependence is unique. We used two markers of dependence, FTCD and exhaled CO concentration. In our study, as in previous studies, for example Aveyard et al. ,36 FTCD predicted the likelihood of achieving abstinence. The ORs were 0.85 (95% CI 0.62 to 1.17) for moderate dependence compared with low dependence and 0.61.(95% CI 0.42 to 0.90) for moderate dependence compared with high dependence. The p-value for trend through those categories is 0.013. Thus, in this population of people who seek help to stop smoking and who are more dependent than the average person who smokes, this marker functions as a predictor of abstinence and might, therefore, be expected to moderate the effect of preloading. However, exhaled CO concentration did not function as a useful predictor of the likelihood of abstinence; compared with a CO concentration of < 10 p.p.m. at baseline, for the categories in Figure 5b, the ORs were 0.67, 0.63, 0.79 and 0.74, with a p-value for trend of 0.84. This may, therefore, explain why exhaled CO concentration did not moderate the association.

Our mediation analysis is complemented by previous analyses in other trials of preloading that examined the effect of preloading on several potential mediators. Unlike previous analyses,12 we found that preloading did reduce both positive and negative reward from smoking, but our study is much larger than the previous studies that have examined these mediators, so these trials may have missed this association. As two previous studies have also discovered,12 we found a small reduction in pre-quit urges to smoke. Most previous trials examined changes in cigarette consumption caused by preloading and, as we found, noted reductions in the pre-quit period. 12 Those trials that examined reduction in dependence reported the same kind of reductions that we observed in this trial. Previously, we concluded that preloading did not appear to reduce craving after quit day,12 but there was clear evidence in this trial that preloading did reduce craving. Although previous studies examined the effect of preloading on potential mediators, none undertook a full mediation analysis, as we have done here. Doing so revealed new insights. Although people’s perception of reward may have changed, the main apparent mechanism seems to be through reduction in the urge to smoke. It is possible that this effect is indeed mediated by reward, but that people’s perception of it may not be very sensitive. Alternatively, the drive to smoke may weaken in smokers saturated with nicotine from an alternative source without any effect on their subjective reactions when they do smoke. The main drive to smoke does not require conscious appreciation for it to be experienced. 98 No previous studies have examined whether or not there is effect modification by strength of dependence on tobacco.

Interpretation

This study and previous literature together have produced clear evidence that preloading reduces the intensity of urges to smoke and that it reduces the intensity of smoking during the pre-quit period. The reduced drive to smoke appears to be the best candidate mechanism for the effect of preloading, with reduced smoke intake being one of its consequences.

This has important implications for clinical practice. If preloading were to be used routinely in NHS Stop Smoking Services, then advisors could monitor its effect using markers of urge strength, asking users whether or not they have experienced reduced urge intensity, and also by measuring exhaled CO concentration, which is routine in NHS clinics. This could allow clinicians to advise their patients to abandon preloading if it appears to be having little effect, confident that the evidence now supports this.

Many trials of treatment for tobacco dependence enrol people who smoke a minimum of 10 cigarettes per day, but around one-third of the population who smoke consume fewer cigarettes than this per day. We enrolled such participants if they were seeking help to quit and smoked at least one cigarette per day, providing they manifested other features of dependence, including difficulty attaining abstinence. This may have contributed to including a greater range of participants than in some trials of pharmacotherapy. Including a wide range of participants should make it easier to detect effect modification between markers of dependence. Although there was no clear evidence of effect modification, both point estimates suggested a greater relative benefit in people with a higher level of dependence. As we did not plan for the study to have power to detect this interaction, it may be that we simply failed to find evidence for an effect, rather than this representing clear evidence against an effect. Given the mechanisms of action of preloading and this evidence together, it would seem appropriate for smoking cessation advisors to consider this strategy in anyone seeking treatment, but perhaps particularly for people with a higher level of dependence.

Summary of main findings

The primary outcome of the cost-effectiveness analysis was the incremental cost per additional case of 6-month prolonged abstinence. The prolonged abstinence rate at 6 months post quit date according to the Russell Standard was 17.5% in the intervention group and 14.4% in the control group, a difference of 3.1% (95% CI –0.3% to 6.4%). Mean total costs, from randomisation to 6 months post quit date, were £978 (SE £105) in the intervention group and £1090 (SE £110) in the control group. The adjusted incremental costs were £4 (95% CI –£188 to £222). The incremental costs per additional 6-month prolonged abstinence were, therefore, £129 (95% CI –£16,527 to £17,782). The wide CI crossed the zero point, which amounts to no clear evidence that the intervention was more cost-effective than the control condition. The analysis of data at 12 months’ follow-up suggested a possible reduction in health service costs in the intervention group (–£233, 95% CI –£747 to £42). This pointed to a potential cost-saving scenario in the long run, given that the abstinence rate at 12 months was not significantly different between arms. Sensitivity analysis did not change the pattern of these results. There were indications that the costs might have been underestimated in the complete-case analysis.

Strengths and limitations

The strength of this analysis lies in the comprehensive analysis of all health and social care costs, thus providing a clear picture for the NHS when deciding on treatment. As in all such studies, however, we suffered from missing data. In particular, people who try to quit smoking with support and fail to do so are always somewhat reluctant to return for follow-up. For the sake of the primary outcome, we maximised the return of data on smoking status among participants who were reluctant to be followed up. This sometimes meant that we excused people from answering the health resource questions and, as a result, these data were more often missing than data on smoking status. As the data showed, people with complete data were more likely to be abstinent, but there is no reason to imagine that health service use differed between arms among people who were not abstinent and this is unlikely to bias the results.

With the complicated nature of health resource use data, it was inevitable that some assumptions had to be made before any analysis could be undertaken. The less than reliable approach of self-reporting only added to the uncertainties. However, short of accessing participants’ usage directly from the providers, it was the best way to collect this information. The assumption that no response equates to no use is generally seen to be compatible with the way that people complete health resource use questionnaires. The assumptions made about monthly prescriptions are less certain. The prescribing patterns varied between GPs and, without more detailed information, it was not possible to estimate the cost of medication more accurately. Collecting these data from participants directly in a trial of this kind would add a considerable burden and probably increase withdrawal rates. Even if this burden could be disregarded, participants’ reports of medication use are often less than satisfactory for the purpose of costing. In spite of these uncertainties, the assumptions were applied to both arms and, therefore, should not bias the results towards either group.

Participants with complete information on health resource use had much lower use than that suggested from the imputed data. This is not surprising: participants with greater health needs may find it more burdensome to complete questionnaires, be less likely to achieve abstinence and be more likely to drop out of follow-up. However, this effect is unlikely to differ between arms.

The data presented are a within-trial analysis of cost-effectiveness. The reason that people try to stop smoking, and the reason the NHS invests in smoking cessation services, is to support long-term abstinence and to avoid the costs of smoking-related illnesses in the future. It is not possible to collect such data in trials, but it is possible to model them and we present these data in Chapter 7. A second issue relates to the design of the trial itself and the constraints that this imposed on the cost-effectiveness analysis. To be able to assess AEs and the mechanism of action of preloading in an unbiased way, those in the control group delayed their quit attempt to the same extent as those in the preloading group. To ensure that people returned to give us these data, we gave behavioural support to those in the control group and set this group up to believe that this would be useful to them. There is no clear evidence that this is the case and, in any case, the support that we gave is commonly incorporated into standard NHS smoking cessation support, which both the intervention group and the control group received later. In this within-trial analysis, we included the cost of the behavioural support in the control group. The NHS decision problem, however, was to assess the difference between preloading and standard NHS smoking cessation support, with only a minimal period of preparation before quitting. Thus, the control group behavioural support sessions would not happen in any future NHS scenario. Assuming that the outcomes remain the same, the simple exclusion of two behavioural support sessions from the control group would result in an increase in the adjusted difference in costs between arms and an increase in the ICER in turn. For the complete-case analysis, the difference in costs between trial arms would increase from £138 to £155, resulting in a modest change in the ICER of around £700, whereas the change in the adjusted difference in costs between arms in the imputed data (from £4 to £17) would lead to an increase in the ICER of £550. However, the assumption that extra behavioural support in preparation to quit has no impact on outcomes cannot be easily made. These numbers are only estimates and further assessment is required to provide supporting or opposing evidence. In addition, the cost-effectiveness analysis appropriately focuses on the primary analysis of the primary outcome. However, this is a biased estimate of the efficacy of preloading because it is confounded by differences in the use of varenicline. Had we used the estimate for the difference in the effect of preloading adjusted for varenicline, then the cost-effectiveness might have more strongly favoured preloading over the control.

Interpretation

This is the first assessment of the cost-effectiveness of nicotine preloading. Indeed, relatively few trials have conducted within-trial analyses of the cost-effectiveness of smoking cessation medication. One comparator is the NHS Stop Smoking Service, which collects data on the cost per person who has quit smoking and remained abstinent for 4 weeks. Statistics on NHS Stop Smoking Services in England April 2014 to March 201565 showed, among local authorities, a cost per person who quit smoking ranging from £98 to £1185, with a mean of £456. The cost per person who quit smoking at 4 weeks in this trial was £501 in the preloading group and £417 in the control group, somewhat in the middle of the distribution. That said, the NHS counts self-reported abstinence as abstinence, which we excluded; if we had included self-reported abstinence, it would reduce the cost per quitter by nearly one-third.

Interpreting the data here is harder because there is no available WTP threshold for 6-month prolonged abstinence; therefore, it is not possible to draw clear conclusions with regard to whether or not the intervention can be seen to be cost-effective. An incremental cost of £129 per additional 6-month abstinence might be considered cost-effective if the policy-makers judge the abstinence to be beneficial, given the impact of smoking cessation on long-term quality of life. What may encourage policy-makers to consider preloading are the data showing that, at 12 months, preloading reduced overall health service costs. In the short term at least, smoking cessation should reduce the demand for health services by reducing the incidence of both minor and major ill-health consequences of smoking. Future modelling may provide further data to support this.

Summary of findings

The smoking cessation costs within the intervention group over the course of the first year were higher than those in the control group, with intervention group costs of £295, compared with control group costs of £265. However, more smokers quit smoking in the intervention group (n = 139) than in the control group (n = 112) and consequently health-care costs associated with smoking were lower in the intervention group over the course of the lifetime. Overall, the total costs were £29 lower in the intervention group. The intervention was also more effective than the control condition, resulting in 14.0% of smokers in the intervention group quitting at 1 year compared with 11.3% of smokers in the control group, and consequently produced more QALYs and life-years. The intervention would be considered cost-effective as it resulted in greater efficacy at a lower cost than the control condition. The results were robust to changes in assumptions regarding discount rates and relapse after the first year of follow-up.

Strengths and limitations

The major strength of this approach is that it builds on the comprehensive within-trial cost-effectiveness assessment presented in Chapter 6. However, it takes the same perspective as people who are stopping smoking: that the main reason to stop smoking is to avoid future smoking-related disease. 99 As such, it better represents the views of possible service users of NHS Stop Smoking Services and of the community at large. The major weakness is that, as with practically all long-term cost-effectiveness studies, the results are modelled on the future likelihood of disease. Confidence in this modelling is supported by the robust epidemiological evidence available on the association between smoking and incidence of and mortality from disease and the difference in risk arising as a result of stopping smoking at different ages. The model has been extensively discussed and described elsewhere (forthcoming supplement in the journal Addiction) and is used by NICE to examine the cost-effectiveness of smoking cessation medications. 67 However, nobody has prospectively validated models of incidence, mortality and health-care expenditure of cohorts of people who continue or stop smoking, so ultimately the data should be regarded as somewhat conjectural. This emphasises the importance of sensitivity analyses and a strength of the findings here is that they appear largely unaltered by both deterministic and probabilistic sensitivity analyses; all answers converged to suggest that preloading is dominant over the comparator in the large majority of model runs.