Small Financial Incentives to Promote Smoking Cessation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Small Financial Incentives to Promote Smoking Cessation (NCT02737566), a randomized na study. The primary outcome is Biochemically-verified Smoking Cessation.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group trial with no masking reported. The registry record lists an enrollment of 320 and a completed status. It identifies the University of Oklahoma as sponsor. The listed study start was 2017-01-30, and the primary completion date was 2022-02-08. The phase is listed as not applicable.

Participants were assigned to standard care plus financial incentives or standard care. In the incentive group, participants were offered counseling and pharmacotherapy and could earn small gift cards for biochemically verified abstinence through 12 weeks after quitting. The standard-care group was offered weekly counseling and pharmacotherapy. The record does not report the incentive amounts or enough detail to characterize adherence to counseling or pharmacotherapy.

The primary outcome was carbon monoxide-verified 7-day point-prevalence abstinence at 26 weeks after the quit attempt. A secondary outcome measured biochemically verified smoking cessation at 12 weeks after the quit attempt. The study summary also describes self-reported tobacco use or abstinence, expired carbon monoxide, and saliva cotinine at 26 weeks, but the posted primary outcome is specifically defined using carbon monoxide verification.

Random assignment supports a comparison of the groups as assigned, but the registry record does not report the randomization sequence method, allocation concealment, stratification, or other implementation details. It also does not report the original sample-size justification, planned statistical model, interim analyses, or a prespecified multiplicity strategy. Those details should not be inferred from the posted outcome counts or planning illustrations.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Biochemically-verified Smoking Cessation, measured over 26 weeks post-quit.

The primary endpoint is the count of participants with carbon monoxide-verified 7-day point-prevalence abstinence at 26 weeks after the quit attempt. The registry definition specifies an intent-to-treat approach and says missing outcomes are counted as smoking. In other words, the outcome concerns whether a participant met the abstinence definition at the assessment, with expired carbon monoxide used for verification.

Point-prevalence abstinence is a snapshot of status over the specified recent period, rather than a measure of uninterrupted abstinence from the quit date through follow-up. That distinction matters when interpreting the result: it describes the endpoint at the 26-week assessment and does not, by itself, describe every participant’s smoking history during the intervening weeks.

Biochemical verification adds an objective measure to an outcome that can otherwise depend on self-report. In general, expired carbon monoxide is a biological measure relevant to recent smoking exposure. The study summary also mentions self-reported tobacco use and saliva cotinine at 26 weeks, but the registry’s primary endpoint identifies carbon monoxide-verified abstinence. The record does not report the specific carbon monoxide threshold used, how testing was conducted, or how discordant self-report and biomarker results were handled.

The endpoint is clinically interpretable as a count of participants meeting the defined abstinence criterion, but its meaning remains tied to the measurement window and verification procedure. It should not be read as a direct measure of long-term cessation beyond the reported assessment.

7. Results Posted in the Registry

• Standard Care: 8.7% (14/161) versus 13.8% (22/159) on control; risk difference -5.1 percentage points (95% CI -12.1 to 1.8), risk ratio 0.63 (0.33–1.18); unadjusted two-proportion z-test p = 0.146.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Biochemically-verified Smoking Cessation

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Standard Care: 11.2% (18/161) versus 28.3% (45/159) on control; risk difference -17.1 percentage points (95% CI -25.6 to -8.6), risk ratio 0.40 (0.24–0.65); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Standard Care than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcome is biochemically verified smoking cessation at 12 weeks after the quit attempt. The broad pattern is that the posted comparison at this earlier follow-up favors the incentive group in direction, while the primary comparison at 26 weeks is less statistically distinct from no difference. This provides a time-specific contrast: the earlier outcome and the later primary endpoint do not convey the same degree of statistical certainty.

The secondary finding is related to, but does not replace, the primary result. It uses the same broad cessation construct at a different follow-up time. An outcome at 12 weeks cannot establish the result at 26 weeks, and neither time point alone describes continuous abstinence over the full interval. The earlier endpoint may be useful for understanding the observed temporal pattern, but the registry record does not report a longitudinal model or a formal comparison of changes over time.

Unadjusted secondary results carry less weight when several outcomes or time points are considered because each additional statistical comparison creates more opportunities for a chance finding. In general, multiplicity adjustment or a prespecified hierarchy can help control that concern, but the registry record does not report such a strategy. The secondary result should therefore be treated as supportive and exploratory in interpretation, rather than as an independent confirmation of the primary finding.

The record lists one secondary outcome and reports no secondary analyses. It does not explain whether other outcomes were planned but not posted, how the secondary comparison was selected, or whether its analysis was prespecified. Those gaps make it difficult to assess the degree to which the posted result reflects a confirmatory test. The overall pattern is informative descriptively, but it does not remove the uncertainty surrounding the primary 26-week comparison.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Biochemically-verified Smoking Cessation

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either meets the defined carbon monoxide-verified abstinence criterion at the 26-week assessment or does not. The registry reports counts and group sizes, then presents comparisons between the randomized groups. Because the outcome is a count of participants meeting a criterion, its interpretation differs from an outcome such as a continuous measurement, for which the analysis would compare means or other summaries of a numeric scale.

What does the risk difference mean?

A risk difference expresses the difference between the proportions meeting the outcome in two groups. It is an absolute comparison, rather than a relative one. The posted comparison uses standard care relative to standard care plus financial incentives: the estimate is -0.051, with a 95% confidence interval from -0.120 to 0.018. Its negative direction indicates that the observed outcome proportion was lower in the standard-care group under that ordering. The interval includes zero, which represents no absolute difference.

The group proportions used in the comparison are reported as 0.138 for standard care plus financial incentives and 0.087 for standard care. These values describe the observed outcome proportions in the respective groups. They should be interpreted alongside the counts, because the counts show how many participants met the endpoint and the group sizes show the denominators used in the comparison.

How do ratios differ from a risk difference?

A risk ratio compares the outcome proportions as a ratio, while an odds ratio compares the odds of the outcome. Ratios use a relative scale; a value of 1 represents no relative difference. The posted risk ratio is 0.628, with a 95% confidence interval from 0.334 to 1.184. The posted odds ratio is 0.593, with a 95% confidence interval from 0.292 to 1.206. Their confidence intervals include 1. These ratio measures can appear different in magnitude from an absolute risk difference because they answer different questions. The registry record does not report a model specification for these estimates.

What does the p-value add?

The unadjusted p-value for the primary comparison is 0.146. In general, a p-value measures how compatible the observed data are with a specified null model, assuming that model and the analysis assumptions hold. It is not a measure of the size or importance of an effect and is not the probability that the null hypothesis is true. It also does not account for the range of values that may be compatible with the data; the confidence interval provides information about that uncertainty.

“Unadjusted” indicates that the reported p-value is not described as adjusted for multiplicity or for other covariates. The registry record does not report the statistical test or model used to calculate the comparison. Consequently, the estimates can be described as posted, unadjusted summaries, but a more specific account of model assumptions or covariate handling is not available in the registry record.

Why is the confidence interval useful?

In general, a confidence interval gives a range of values that are reasonably compatible with the observed data under the method used to construct it. It conveys uncertainty around the point estimate and helps distinguish a narrowly estimated result from one with substantial uncertainty. A confidence interval is not a guarantee that the true value lies within its limits, nor does it assign a probability to a particular effect after the data have been observed.

For the primary risk difference, the interval extends from a negative value to a positive value and includes zero. This means the posted analysis does not rule out no difference, and it also leaves room for effects in either direction. The ratio confidence intervals likewise include the no-difference value of 1. These features are consistent with the unadjusted p-value and emphasize that the primary comparison is uncertain rather than conclusive.

What can be said about analysis populations and assumptions?

The endpoint description explicitly identifies an intent-to-treat approach and specifies that missing outcomes are counted as smoking. This treatment of missing outcomes is part of the endpoint definition, but the record does not provide the number of missing measurements, reasons for missingness, or sensitivity analyses using alternative assumptions. The primary analysis population is therefore described at the level of the stated intent-to-treat rule, not through a detailed account of participant flow or missing-data diagnostics.

The registry record does not report an adjusted primary analysis, a statistical model, the test used for the p-value, interim analyses, or the trial’s original sample-size justification. These omissions limit assessment of whether the posted comparisons followed a fully prespecified plan. They do not change the arithmetic meaning of the reported counts and estimates, but they constrain how much can be concluded about the analysis process.

In general, binary outcomes can be summarized through counts, proportions, absolute differences, and relative measures. Each conveys a different aspect of the comparison. Reading the counts, point estimate, confidence interval, and p-value together is more informative than focusing on any one statistic. The randomized allocation helps frame the comparison between assigned groups, while the endpoint definition and missing-outcome rule determine what the result measures.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate the group difference. The primary risk-difference estimate is -0.051, and its 95% confidence interval runs from -0.120 to 0.018. Because the interval includes zero, the result is compatible with no risk difference under the reported analysis. It also extends to values on both sides of zero, so the data do not pin down the direction of the underlying difference precisely.

The relative measures tell a similar story about uncertainty. The risk ratio is 0.628, with a 95% confidence interval from 0.334 to 1.184, and the odds ratio is 0.593, with a 95% confidence interval from 0.292 to 1.206. Both intervals include 1, the no-difference value for a ratio. The estimates point in the same general direction as the observed counts, but their intervals leave substantial uncertainty about the size of any group difference.

In general, a confidence interval is more useful than a point estimate alone because it conveys the range of estimates compatible with the data and method. It is not a range guaranteed to contain the true effect, and its interpretation depends on the analysis assumptions. The registry record does not report enough methodological detail to assess every assumption behind interval construction.

The primary confidence interval should not be interpreted as evidence of equivalence. Demonstrating equivalence would require an appropriate prespecified margin and analysis, neither of which is reported in the registry record. Nor should lack of statistical distinction be read as proof that the intervention and comparator have the same effect. The interval indicates uncertainty, not sameness.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm for the binary outcomes, not total event counts. The planning illustration is based on the observed effect and uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Its rows consider detecting 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm that would be needed, under those assumptions, for an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding planning number for a 90% chance. These are design concepts: power is the probability of obtaining a result meeting a chosen criterion when a particular effect is assumed to be present.

The planning figures increase as the target effect becomes smaller. A smaller difference is harder to distinguish from random variation, so more participants are generally needed to detect it at the same significance level and target power. The displayed estimates are tied to the observed effect in this trial and to the stated assumptions; changing those assumptions or the effect size would change the planning result.

This is not observed power. It is a forward-looking planning illustration, not a measure of how likely the completed trial was to find a difference after its results were known. The figures should not be read as evidence that the trial was originally designed using these assumptions, because that design information is not reported in the registry record.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.138; treatment proportion p₁ = 0.087; average p̄ = 0.113.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4471 = 0.8764.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4457 = 0.3751.
4. n = (0.8764 + 0.3751)² / (-0.0514)² = 592.6, rounded up to 593 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.138364779874214                          # control proportion
p1 <- 0.0869565217391304                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(2737566)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 593 (80% power), 793 (90% power)
 75% of observed effect: n per arm = 1,107 (80% power), 1,481 (90% power)
 50% of observed effect: n per arm = 2,607 (80% power), 3,490 (90% power)
power.prop.test: 592.6 
Simulated power at n = 593 per arm: 0.803 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is identified as intent-to-treat, with missing outcomes counted as smoking. This is an explicit rule for handling missing primary endpoint data. The registry record does not report how many participants had missing carbon monoxide assessments, whether missingness differed between groups, or why any outcome was unavailable. It also does not report sensitivity analyses that test alternative assumptions about missing outcomes.

Counting missing participants as smoking is a conservative outcome rule in the sense that an unobserved outcome is not treated as abstinent. However, it does not eliminate all concerns about missing data. The interpretation still depends on the amount and pattern of missingness, and the record does not provide enough detail to evaluate those features. The available results should therefore be understood according to the stated rule, without assuming that missingness was absent or evenly distributed.

The registry record does not report a multiplicity plan, such as an adjustment for testing more than one outcome or a hierarchy that gives the primary endpoint priority over secondary outcomes. The primary outcome is clearly designated, which distinguishes it from the secondary outcome, but the record does not describe how the overall chance of false-positive findings was controlled across analyses. The secondary comparison is reported as unadjusted, so it warrants more caution than a result supported by a stated multiplicity procedure.

The primary comparison is also reported without a model description or covariate-adjusted analysis. The record does not report interim analyses, the original sample-size justification, or detailed analysis-population rules beyond the primary endpoint’s intent-to-treat statement. It does not report participant flow or reasons for exclusion from particular measurements. These omissions do not make the posted counts unusable, but they limit evaluation of whether all analyses followed a prespecified plan and how robust the findings are to analytic choices.

In general, preregistration and clear reporting of analysis populations, missing-data procedures, and multiplicity plans help readers distinguish confirmatory analyses from exploratory ones. Where such details are not reported in the registry record, the conclusions should remain closely tied to the outcomes and unadjusted comparisons that are posted.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event figures report zero affected participants in each group: zero among 159 participants assigned to standard care plus financial incentives and zero among 161 assigned to standard care. The registry record also lists zero deaths in each group. These are observed counts for the groups at risk as recorded; they do not establish that serious events could not occur or that the groups have identical safety profiles.

For other adverse events, the registry lists 2 affected participants among 159 in the incentive group and 2 among 161 in the standard-care group. These counts should be read as reported participant counts, not as a complete description of event types, severity, duration, or relation to treatment. No top serious adverse event terms are listed.

The registry record does not report the safety observation period, definitions used for event categories, event-level details, or a statistical comparison of adverse events. With small observed counts, the figures provide limited information about uncommon harms. They are descriptive reporting, not a basis for concluding that one group is safer or that no risk exists.

16. What the Result Does, and Does Not, Mean

The primary result describes a randomized comparison of assignment to standard care plus financial incentives versus standard care for carbon monoxide-verified 7-day point-prevalence abstinence at 26 weeks after the quit attempt. The observed counts were 22 of 159 in the incentive group and 14 of 161 in the standard-care group. The posted risk difference is -0.051 when expressed as standard care relative to the incentive group, and its 95% confidence interval includes zero. The unadjusted p-value is 0.146.

These statistics do not establish a clear difference at the primary follow-up, but they also do not establish that the groups were equivalent. The confidence interval spans no difference and effects in either direction. The correct interpretation is that the primary estimate is uncertain, not that the intervention has been shown to work or not work. The data describe this trial’s participants, endpoint definition, and follow-up assessment.

The secondary outcome at 12 weeks has a more statistically distinct unadjusted comparison and points in the same direction as the observed primary counts. That earlier result may help describe the pattern across follow-up times, but it cannot substitute for the primary endpoint or prove that an effect persisted to the later assessment. Because no multiplicity strategy is reported, the secondary result deserves cautious interpretation.

More generally, a trial’s estimates are not direct statements about every individual participant, and a group-level association does not explain the mechanism behind an outcome. The study summary describes an interest in treatment mechanisms and contextual factors, but the posted analyses do not report results for those questions. The registry record also does not provide enough detail to assess generalizability to other clinical settings or populations.

The endpoint is a point-prevalence measure verified by carbon monoxide, with missing outcomes counted as smoking under the stated intent-to-treat rule. It is not a record of continuous abstinence across the entire period. Interpretation should remain within those measurement boundaries and should account for the uncertainty in the primary comparison and the limited detail on analysis methods.

17. Why This Trial Matters Statistically

This trial illustrates why statistical interpretation should combine event counts, an effect estimate, its confidence interval, and a p-value. The primary comparison’s counts lean in one direction, but the risk-difference interval includes zero and the unadjusted p-value is 0.146. Looking only at the direction of the point estimate would understate uncertainty; looking only at whether a p-value crosses a threshold would discard information about the range of effects compatible with the data.

The result also demonstrates the importance of distinguishing an absolute effect from relative measures. The risk difference, risk ratio, and odds ratio summarize the same binary outcome on different scales. Their interpretation depends on the comparison direction and on their respective no-difference values. They are not separate pieces of evidence that can simply be counted as multiple confirmations.

The trial has an earlier secondary assessment as well as a later primary assessment. Their differing statistical patterns underline why follow-up time and endpoint hierarchy matter. A finding at one time point does not automatically answer the primary question at another time point, and unadjusted secondary tests require caution when a study considers multiple outcomes.

Finally, the record distinguishes the trial’s observed results from an illustrative sample-size exercise based on the observed effect. Planning numbers can help explain how target effect size and desired power influence sample requirements, but they are not the trial’s original design rationale and are not observed power. Keeping that distinction clear prevents a retrospective calculation from being mistaken for a documented protocol decision.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record offers limited detail about the trial’s implementation and analysis. It does not report the randomization sequence method, allocation concealment, or the statistical model and test used for the posted comparisons. The trial’s original sample-size justification, interim analyses, and prespecified multiplicity strategy are also not reported. These omissions restrict assessment of how closely the posted results match a planned analysis.

The primary endpoint uses carbon monoxide verification, but the record does not report the threshold or testing procedures. It does not describe how discrepancies between self-report and biochemical measures were resolved. Although the study summary mentions saliva cotinine and self-reported tobacco use, the posted primary endpoint is defined through carbon monoxide verification, and the additional measurement details are not available in the record.

The intent-to-treat endpoint description specifies that missing outcomes are counted as smoking, but the number and pattern of missing measurements are not reported. Reasons for missing data and sensitivity analyses are also not reported. As a result, readers cannot evaluate how strongly the primary estimate depends on the stated missing-outcome rule.

The arm description does not include the incentive amounts, and the registry record does not provide detailed information about treatment uptake or adherence. It also does not report a detailed profile of eligibility criteria or participant characteristics in the primary outcome entry. These limits make it difficult to assess which features of the intervention or population may be most relevant to the observed comparison.

Finally, the primary endpoint is a point-prevalence assessment at 26 weeks, not a measure of uninterrupted abstinence across follow-up. The posted statistics do not establish effects beyond the reported time point, identify mechanisms, or support conclusions about populations and settings not described in the record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Small Financial Incentives to Promote Smoking Cessation — NCT02737566.
• Registry record last updated 2026-06-18; status last verified 2026-05.
• Results first posted 2023-04-20.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed, randomized, parallel-group trial sponsored by the University of Oklahoma, with enrollment of 320 and no masking reported. It compared standard care plus the opportunity to earn small gift cards for biochemically verified abstinence through 12 weeks after quitting with standard care alone. Both groups were offered smoking-cessation counseling and pharmacotherapy.

The primary outcome was carbon monoxide-verified 7-day point-prevalence abstinence at 26 weeks after the quit attempt, analyzed by the stated intent-to-treat rule with missing outcomes counted as smoking. The posted primary comparison is unadjusted, and its confidence interval includes no difference. A secondary outcome assessed biochemically verified cessation at 12 weeks. The record does not report the original sample-size rationale, detailed statistical plan, multiplicity strategy, or full missing-data information.