Combination Bupropion / Varenicline for Smoking Cessation in Male Smokers: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Combination Bupropion / Varenicline for Smoking Cessation in Male Smokers (NCT01806779), a randomized phase 2 study. The primary outcome is Number of Participants Completing Continuous Four-week Abstinence From Smoking Between the 8-week and 11-week Post Quit Day Visits.

2. Clinical Question

The registry record frames the study as an attempt to replicate prior findings from the investigators’ center about combination treatment. That statement describes the investigators’ rationale; it is not evidence about the results of this trial. The posted primary comparison is an unadjusted comparison of the two named groups. It does not establish that any difference was caused by the treatment combination, and the uncertainty around the comparison matters when interpreting the observed counts.

3. Trial Design

This was a Phase 2, randomized, double-blind, parallel-group trial sponsored by Duke University. The registry record lists the study as completed, with a start date of 2013-03 and primary completion in 2014-12. The total enrollment recorded was 376. The primary comparison concerns participants assigned to Chantix or Chantix + Zyban; the registry’s adverse-event information also lists a Nicotine Patch group.

The primary endpoint is recorded as a count of participants who met an abstinence definition. In the Chantix group, 41 of 90 participants met that definition; in the Chantix + Zyban group, 38 of 84 did. These arm-level denominators belong to the posted primary comparison. They should not be added together to infer the size of a distinct analysis population or to reconcile the overall enrollment figure.

The registry lists nicotine patches as an intervention and describes treatment after switching from nicotine replacement therapy. The descriptions available for the Chantix and combination arms refer to treatment timing around the target Quit Day, but the record does not provide a complete regimen in this discussion available for this analysis. The full original protocol, including the trial’s original design assumptions and detailed allocation procedures, is not reported in the registry record.

Randomization is intended to make treatment groups comparable on average, while double masking is intended to limit the influence of treatment knowledge on participants’ reports and other study procedures. These are general features of trial design, not proof that all sources of bias were eliminated. The registry record does not report enough detail to assess how masking was maintained or whether it was successful.

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.

Before assignment: Of the 376 subjs. enrolled, 179 were withdrawn by study staff or withdrew voluntarily from further participation prior to the 1st study visit (V1). 197 subjs. met all study criteria, attended V1 \& given NRT for 1 week; 176 subjs. attended V2 \& completed SE quest.; 2 subjs. dropped out during this visit before randomization; 174 subjs. randomized.

Overall Study

Reasons for not completing this period:

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 Number of Participants Completing Continuous Four-week Abstinence From Smoking Between the 8-week and 11-week Post Quit Day Visits, measured over Period between 8-week and 11-week visits post target Quit Day.

The primary endpoint counts participants who achieved continuous four-week abstinence from smoking during the period between the 8-week and 11-week visits after the target Quit Day. The registry defines success using a composite: at the 11-week study visit, participants had to report no smoking between the 8-week and 11-week visits and have expired-air carbon monoxide below 10 ppm. Drop-outs were considered non-abstinent under the stated intent-to-treat criterion.

Combining self-report with a carbon monoxide measurement makes the endpoint depend on both reported smoking behavior and an objective measurement at the study visit. Requiring abstinence across the specified period distinguishes this outcome from a point-prevalence measure, which asks about smoking status over a shorter reference period. That distinction matters when interpreting other outcomes in the trial: the secondary measure of seven-day point abstinence at 6 months does not use the same abstinence window as the primary endpoint.

The endpoint is clinically interpretable as a count of participants meeting the study’s specified abstinence criteria, but it does not capture every aspect of smoking behavior or establish long-term abstinence. Its interpretation also depends on the stated rule for handling drop-outs. Other details, such as procedures for missing carbon monoxide measurements among participants who attended the visit, are not reported in the registry record.

7. Results Posted in the Registry

• Chantix + Zyban: 45.2% (38/84) versus 45.6% (41/90) on control; risk difference -0.3 percentage points (95% CI -15.1 to 14.5), risk ratio 0.99 (0.72–1.38); unadjusted two-proportion z-test p = 0.966.

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.

Number of Participants Completing Seven-day Point Abstinence From Smoking at 6 Months Post Quit Day

• 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:
  • Chantix + Zyban: 22.6% (19/84) versus 23.3% (21/90) on control; risk difference -0.7 percentage points (95% CI -13.2 to 11.8), risk ratio 0.97 (0.56–1.67); unadjusted two-proportion z-test p = 0.911.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Chantix + Zyban and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants Completing Continuous Abstinence From Smoking Between Quit Day and 11-week Post Quit Day Visit

• 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:
  • Chantix + Zyban: 17.9% (15/84) versus 23.3% (21/90) on control; risk difference -5.5 percentage points (95% CI -17.5 to 6.5), risk ratio 0.77 (0.42–1.38); unadjusted two-proportion z-test p = 0.373.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Chantix + Zyban and the control. The interval gives the range of effects that remain compatible with the data.

The two posted secondary outcomes use different abstinence definitions and time windows: seven-day point abstinence at 6 months after Quit Day, and continuous abstinence from Quit Day through the 11-week visit. Across the primary and secondary comparisons, the estimated risk differences are negative for Chantix + Zyban relative to Chantix. The confidence intervals for the secondary comparisons also include zero. Taken together, the posted estimates do not show a consistent pattern of higher abstinence in the combination group, but their uncertainty does not establish that the groups are equivalent.

The secondary outcomes add context because they examine abstinence at a later point and across a longer period than the primary endpoint. They are not interchangeable with the primary outcome: point abstinence at 6 months concerns a short reference window, whereas continuous abstinence requires meeting a criterion over an extended interval. Different endpoint definitions can produce different event counts and may answer different questions about smoking behavior.

The secondary comparisons should carry less weight than a prespecified primary comparison when their place in the analysis plan and their multiplicity handling are unclear. The registry record lists the secondary outcomes but does not report a multiplicity plan or a separate set of reported analyses. In general, evaluating several outcomes creates more opportunities for chance findings, so isolated secondary results are best interpreted as exploratory unless their role and analysis were specified in advance.

These secondary outcomes do not erase the uncertainty in the primary comparison or supply a definitive answer about the treatment contrast. Their value is descriptive: they show whether the direction of estimates is broadly similar across the posted abstinence measures, while the confidence intervals indicate that the comparisons remain uncertain. The registry record does not report additional analyses that would clarify whether these measures were intended to support confirmatory conclusions.

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

• Number of Participants Completing Seven-day Point Abstinence From Smoking at 6 Months Post Quit Day
• Number of Participants Completing Continuous Abstinence From Smoking Between Quit Day and 11-week Post Quit Day Visit

9. Statistical Interpretation

10. Statistical Methods Explained

For a binary outcome, each participant either meets the stated event definition or does not. Here, the event is completing the primary abstinence definition. The registry posts counts of participants meeting the definition and the corresponding arm denominators. A useful way to compare such groups is to calculate the event risk in each group and express the difference as the risk in the combination group minus the risk in the Chantix group. This risk difference is on the absolute scale: it describes how far apart the groups’ event proportions are, rather than comparing them as a ratio.

The posted primary risk difference is slightly negative, meaning the observed event proportion is lower in the combination group than in the Chantix group. The estimate is close to zero. The p-value for this unadjusted comparison is 0.966. Because the confidence interval includes zero, the data do not distinguish a difference in either direction from no difference at the conventional level indicated by the interval. This is not a demonstration that the groups are equivalent.

What does a confidence interval communicate?

In general, a confidence interval conveys statistical uncertainty around an estimate under the assumptions of the method used. A wider interval indicates less precision: a broader range of values remains compatible with the observed data and the method. An interval that includes zero for a risk difference includes no difference as one compatible value. It may also include differences in both directions. The interval should therefore be read alongside the point estimate, not as a pass-or-fail result on its own.

A confidence interval does not assign a probability to the true effect being inside the particular calculated interval. Nor does it account automatically for every uncertainty that matters to interpretation. For example, it does not correct for missing outcomes, an inappropriate outcome definition, bias in measurement, or selective reporting unless those issues are addressed by the analysis and its assumptions.

What does the p-value add?

In general, a p-value measures how incompatible the observed data are with a specified null model, assuming that model and the analysis assumptions hold. A large p-value does not establish the null model as true. It can arise when the true difference is small, when data are noisy, or when the comparison is not precise enough to distinguish plausible effects. A p-value also does not measure the size or clinical importance of an effect. For that reason, the estimate and its confidence interval are central to interpretation, with the p-value as a related summary.

The p-value posted for the primary comparison is unadjusted. It should not be interpreted as correcting for the number of outcomes or comparisons considered. Whether a multiplicity adjustment was planned or used is not reported in the registry record. General statistical practice treats multiplicity as relevant when several outcomes or comparisons are tested, because repeated testing can increase the chance of at least one apparently notable result.

Why use a risk difference?

In general, the risk difference is intuitive because it compares event proportions on an absolute scale. Relative measures, such as a risk ratio or odds ratio, describe the comparison differently and can give a different impression of the magnitude, especially when event risks are not small. The registry posts relative measures for the primary comparison as well, but the absolute-scale risk difference directly answers how far apart the two observed event proportions are. No single effect measure removes the need to consider its uncertainty and the endpoint definition.

The trial’s endpoint is binary, but the recorded outcome is a count of participants with the event. It is not a continuous measurement with a mean and standard deviation. The record therefore does not report a dispersion measure for this outcome. General methods for continuous outcomes, such as comparing group means, would not describe the primary endpoint as recorded.

What does randomization contribute?

In general, random assignment helps balance measured and unmeasured characteristics between groups in expectation. It does not guarantee that the groups will be identical in a particular trial, and it does not by itself ensure unbiased results if follow-up, outcome ascertainment, or analysis differs between groups. Double masking can reduce some influences of treatment awareness, but the registry record does not report details that would establish how masking was maintained. The posted summary does not include baseline characteristics or a description of adjustment for them.

The primary endpoint description specifies an intent-to-treat criterion in which drop-outs count as non-abstinent. In general, this rule keeps participants who leave the study from simply disappearing from the outcome definition. It does not by itself resolve every missing-data concern. For example, the registry record does not report how missing visit measurements were handled when a participant was not classified as a drop-out, or whether sensitivity analyses examined alternative assumptions.

The posted comparison is based on summary counts and includes no reported separate adjusted analysis. It is therefore best understood as the unadjusted comparison attached to the registry’s primary outcome. Statistical summaries do not reveal every detail of trial conduct, and the registry record does not report the full analysis plan, the sample-size justification, or an interim-analysis plan.

11. Confidence Intervals and Precision

The primary estimate is close to zero, but the confidence interval spans zero and extends in both directions. This means that the posted data are compatible with no difference and with a range of differences favoring either group. The unadjusted p-value, 0.966, is consistent with the lack of a clear separation in the primary comparison. The interval is the more direct guide to how much uncertainty remains about the size and direction of the effect.

Precision is not the same as whether a result is statistically significant. A precise estimate can be close to zero, while an imprecise estimate can fail to rule out effects that might matter. Whether the range compatible with the data is narrow enough for a decision depends on what differences would be important. A clinically meaningful threshold for this endpoint is not reported in the registry record.

The arm counts are modest in the context of the very small estimated difference, and the interval is broad relative to that estimate. The registry record does not report the original sample-size justification, the target effect used in planning, or the intended precision. Thus, the posted comparison cannot establish whether the trial was designed to resolve a small difference. The later planning illustrations are based on the observed effect and are not a substitute for the trial’s original design rationale.

In general, confidence intervals reflect sampling uncertainty under the statistical method and assumptions used. They do not account automatically for bias, selective reporting, deviations from the protocol, or uncertainty about whether the endpoint fully represents the outcome of interest. Precision should therefore be considered together with the endpoint definition, missing-data procedures, and the limitations of the registry record.

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.

Read each planning value as participants per arm, not as a total across the trial. The registry’s planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is specified as a fraction of the observed effect. These are planning illustrations based on the observed comparison; the original trial’s own sample-size assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% power column gives the corresponding planning quantity for a design with a 90% chance. In general, greater target power requires more participants when other assumptions remain unchanged. Likewise, planning for 75% of the observed effect or 50% of the observed effect means targeting a smaller difference than the observed one; smaller effects are harder to distinguish from random variation and require more participants.

For the primary outcome, the figures are 386,101 participants per arm for 80% power and 516,880 participants per arm for 90% power when planning for 100% of the observed effect. Planning for 75% of the observed effect gives 686,504 and 919,033 participants per arm, respectively. Planning for 50% gives 1,544,859 and 2,068,127 participants per arm, respectively. The very large values reflect the small observed difference used as the planning target, not an independently established treatment effect.

These figures are not observed power. Observed power is not a useful replacement for interpreting the estimate and confidence interval after a trial; the planning figures instead illustrate how sample size changes under specified assumptions. The sample-size assumptions used for the trial itself are 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 = 0.456; treatment proportion p₁ = 0.452; average p̄ = 0.454.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7041 = 1.3800.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7041 = 0.5926.
4. n = (1.3800 + 0.5926)² / (-0.0032)² = 386,100.9, rounded up to 386,101 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 <- 0.455555555555556                          # control proportion
p1 <- 0.452380952380952                          # 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(1806779)
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 = 386,101 (80% power), 516,880 (90% power)
 75% of observed effect: n per arm = 686,504 (80% power), 919,033 (90% power)
 50% of observed effect: n per arm = 1,544,859 (80% power), 2,068,127 (90% power)
power.prop.test: 386100.9 
Simulated power at n = 386,101 per arm: 0.797 (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 registry record identifies a primary endpoint and lists secondary outcomes, but it does not report a multiplicity-adjustment plan. Multiplicity arises when a study assesses more than one outcome or makes more than one comparison. In general, the more tests considered, the greater the chance that at least one result will appear notable by chance alone. Adjustments or a prespecified hierarchy can address this issue, but the record does not say whether either approach was part of the trial’s analysis plan.

The posted unadjusted p-values should therefore be read as results for their individual comparisons, not as values corrected for the full set of outcomes. The primary result remains the principal comparison because the endpoint is designated primary in the registry. Secondary results can be informative, but without a reported testing strategy they are less secure as confirmatory evidence. The registry record does not report interim analyses or stopping rules.

The primary endpoint description specifies an intent-to-treat rule: drop-outs are considered non-abstinent. This is an explicit missing-outcome convention for drop-outs, but the record does not report further detail about missing data, including how absent measurements were treated in other circumstances. It also does not report sensitivity analyses that would assess whether conclusions change under alternative assumptions about missing outcomes.

The registry record does not report a separate adjusted analysis, a detailed analysis population definition beyond the primary endpoint’s stated intent-to-treat criterion, or the original analysis plan. Those omissions limit assessment of whether participants were analyzed according to randomized assignment, how protocol deviations were treated, and whether any prespecified covariates were included. The posted summary remains interpretable as an unadjusted comparison of the recorded group counts, but it cannot answer these methodological questions.

In general, missing outcomes can affect a binary abstinence endpoint because assumptions about participants whose status is unknown influence how event counts are interpreted. Counting drop-outs as non-abstinent is one stated rule, not proof that missingness has no effect. The registry record does not report enough information to evaluate the potential impact of other missing information or to determine whether the analysis population and procedures matched the original protocol.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: allergic reaction to chantix or zyban (1.2%), left sided weakness, headache, blurred vision (1.2%), non-cardiac chest pain & right ventricular hypertrophy (1.1%), jaw & upper extremity fracture due to an accident (1.1%), copd and reactive airway disease (1.1%).

The serious adverse-event figures are counts, with an at-risk count shown for each listed group. The registry records 3 serious adverse events among 90 at risk in the Chantix group, 2 among 84 at risk in the Chantix + Zyban group, and 0 among 197 at risk in the Nicotine Patch group. These are descriptive totals; they do not by themselves establish that an event was caused by a study treatment or support a reliable comparison of safety between groups.

The record also lists other adverse events: 39 among 87 at risk in the Chantix group, 53 among 83 at risk in the Chantix + Zyban group, and 57 among 176 at risk in the Nicotine Patch group. The serious-event terms listed include Allergic Reaction to Chantix or Zyban and Left sided weakness, headache, blurred vision, each recorded as 1.2%. Other listed terms are recorded as 1.1%. These terms and percentages describe the registry entries; they should not be interpreted as treatment-specific rates without further information about attribution and event reporting.

Deaths are not reported in the registry record. The record does not provide enough detail to determine event severity beyond the listed classifications, timing, treatment attribution, or whether participants could contribute more than one event. The group counts are therefore best read as a safety description, not as a causal estimate or a basis for ranking treatments.

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

The primary comparison describes continuous abstinence according to the trial’s specified self-report and carbon monoxide definition. The recorded counts were similar across the two groups, and the posted risk-difference estimate is close to zero. Its confidence interval includes zero and extends in both directions, while the unadjusted p-value is 0.966. Together, these results do not provide clear evidence of a difference in this comparison, but they do not prove that the regimens are equivalent.

The results do not establish that adding Zyban improves abstinence, nor do they establish that it cannot have an effect. A conclusion of equivalence would require a prespecified margin and an analysis designed to evaluate that question; neither is reported in the registry record. A nonsignificant result is not evidence that the true difference is exactly zero.

The study addresses male smokers with nicotine dependence and uses specific abstinence outcomes and follow-up windows. Its findings should not automatically be generalized to other populations, treatment regimens, settings, or longer-term outcomes. The posted primary endpoint assesses abstinence during the period between the 8-week and 11-week visits, while one secondary measure assesses seven-day point abstinence at 6 months. Neither outcome alone captures every dimension of cessation or establishes what happens outside the recorded follow-up.

Interpretation also depends on how participants were followed and how missing measurements were handled. The primary endpoint’s stated rule classifies drop-outs as non-abstinent, but other missing-data procedures and sensitivity analyses are not reported in the registry record. The record also lacks the original sample-size justification, details of multiplicity handling, and a reported adjusted analysis. Those gaps limit how much can be concluded from the posted summary.

In general, trial results are estimates with uncertainty rather than guarantees about outcomes for an individual. The data describe the participants and endpoint represented in this randomized comparison. They do not constitute medical advice, establish causation beyond the assumptions of the trial, or demonstrate that a treatment works or does not work.

17. Why This Trial Matters Statistically

This trial is statistically informative because it places an observed comparison beside its uncertainty. The group counts alone could tempt a reader to focus on which count is larger, but the risk-difference estimate is close to zero and its confidence interval spans no difference. The unadjusted p-value is 0.966. Reading the estimate, interval, and endpoint together gives a more careful account than treating the p-value as a verdict.

The record also illustrates why endpoint definitions matter. Continuous abstinence between specified visits is not the same outcome as seven-day point abstinence at 6 months. These measures have different windows and answer different questions, so their results should not be combined into a single undifferentiated claim about cessation.

Another statistical lesson concerns planning. The sample-size illustrations use fractions of the observed effect and show that planning to detect smaller effects requires more participants. Because the observed primary difference is close to zero, the illustrations produce very large planning values. They are not the trial’s original sample-size justification and are not observed power. The record does not report the original design assumptions, so the illustrations cannot establish whether the trial had adequate planned precision for a clinically important difference.

Finally, the record highlights the value of transparent analysis plans. The primary endpoint and a drop-out rule are stated, but multiplicity handling, detailed missing-data procedures, and a separate adjusted analysis are not reported. Those details would help readers distinguish confirmatory from exploratory findings and evaluate how robust the estimates are to analysis choices. The posted results support a cautious description of the comparison, not a definitive claim about treatment benefit or equivalence.

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 does not report the original sample-size justification or the clinically important difference the trial was intended to detect. Without those details, the observed uncertainty cannot be compared with a prespecified target for precision or used to judge whether the study was designed to address a small effect.

The record identifies the primary endpoint and secondary outcomes but does not report how multiplicity was handled. It also does not report an interim-analysis plan, stopping rules, or a separate adjusted analysis. The unadjusted comparisons should therefore not be treated as multiplicity-adjusted or covariate-adjusted results.

The endpoint description states that drop-outs were considered non-abstinent, but other missing-data procedures and sensitivity analyses are not reported. The available information does not fully describe the analysis population or how the primary comparison denominators relate to the overall enrollment and the Nicotine Patch group listed in safety information. The posted counts should be interpreted as the comparison-specific summaries recorded for the two primary arms.

The registry’s arm descriptions do not provide a complete treatment regimen in this discussion available for this analysis. That limits assessment of treatment exposure and reproducibility from the registry record alone. The record also does not report baseline characteristics or details sufficient to assess how well masking was maintained, adherence, or protocol deviations.

Finally, the primary endpoint measures abstinence over a defined interval and uses both self-report and an expired-air measurement at the 11-week visit. It does not establish longer-term continuous abstinence. The secondary outcomes use different windows, and the registry record does not report additional analyses to reconcile those measures. These limitations support a cautious, endpoint-specific interpretation of the posted results.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Combination Bupropion / Varenicline for Smoking Cessation in Male Smokers — NCT01806779.
• Registry record last updated 2016-01-18; status last verified 2015-10.
• Results first posted 2015-10-08.
• 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

NCT01806779 is a completed, randomized, double-blind, parallel Phase 2 study sponsored by Duke University. It enrolled 376 participants and concerned smoking cessation in male smokers with nicotine dependence. The registry lists Chantix, Zyban, and nicotine patches as interventions.

The primary outcome was the number of participants meeting a continuous four-week abstinence definition between the 8-week and 11-week post-Quit Day visits. The primary comparison reports 41 of 90 in the Chantix group and 38 of 84 in the Chantix + Zyban group. The posted risk-difference estimate is close to zero, its confidence interval includes zero, and the unadjusted p-value is 0.966.

The registry lists two secondary abstinence outcomes and descriptive adverse-event counts. The original sample-size rationale, multiplicity plan, detailed procedures for missing data, and separate adjusted analysis are not reported in the registry record.