A Study To Evaluate The Efficacy And Safety Of Varenicline Compared To Placebo For Smoking Cessation Through Reduction: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study To Evaluate The Efficacy And Safety Of Varenicline Compared To Placebo For Smoking Cessation Through Reduction (NCT01370356), a randomized phase 4 study. The primary outcome is Percentage of Participants With Carbon Monoxide (CO) Confirmed 10-Week Continuous Abstinence (CA) From Smoking.

2. Clinical Question

3. Trial Design

This was a Phase 4, multinational, randomized, double-blind, placebo-controlled, parallel-group study sponsored by Pfizer. The registry record lists the study as completed, with enrollment of 1510. The recorded study start was 2011-07 and primary completion was 2013-07. Participants were assigned to varenicline or placebo. Further information about the randomization sequence, allocation concealment, masking procedures, treatment duration, adherence, or accompanying smoking-cessation support is not reported in the registry record.

The primary efficacy analysis used the Full Analysis Set, which the registry record also calls the Intent-to-Treat population and defines as all randomized participants. The posted primary arm results are 32.1% for varenicline and 6.9% for placebo. The arm sizes displayed with those results are 760.0 and 750.0, respectively. These results concern the prespecified primary outcome as described in the record: carbon-monoxide-confirmed continuous abstinence over Week 15 through Week 24.

The study also posted four secondary smoking-cessation outcomes, including shorter-term abstinence, longer-term abstinence, and point-prevalence measures. Those outcomes cover different periods and definitions, so they complement rather than replace the primary outcome. The registry record does not report the original sample-size justification, the complete statistical analysis plan, or whether interim analyses were planned or conducted. Details about participant flow, losses to follow-up, and protocol deviations are also not reported in the registry record.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set was referred to as the Intent-to-Treat (ITT) population and was defined as all randomized participants. The ITT population was the primary analysis set for the efficacy analyses in this 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 Percentage of Participants With Carbon Monoxide (CO) Confirmed 10-Week Continuous Abstinence (CA) From Smoking, measured over Week 15 - 24.

The primary endpoint was the percentage of participants with carbon-monoxide-confirmed continuous abstinence from smoking during Week 15 through Week 24. To meet the stated abstinence definition, participants had to report no smoking and no use of nicotine-containing products since their last study visit or contact on the Nicotine Use Inventory. The record also required confirmation by expired carbon monoxide at clinic visits during the specified period, using a threshold described as CO < 10 ppm. It states that missing CO was imputed as negative, with the threshold written as CO ≤ 10 ppm.

A continuous-abstinence endpoint asks whether abstinence was maintained across a defined interval, rather than whether a participant was abstinent at one isolated assessment. This makes the measure relevant to the study’s aim of evaluating quitting through reduction. Carbon-monoxide confirmation adds an objective measure alongside participant reports, although it does not by itself establish every aspect of smoking or nicotine-product use throughout the interval. The registry record does not report additional details on the assessment schedule, the handling of missing self-reports, or other endpoint adjudication procedures.

7. Results Posted in the Registry

• Varenicline: 32.1% (244/760) versus 6.9% (52/750) on control; risk difference 25.2 percentage points (95% CI 21.4 to 29.0), risk ratio 4.63 (3.49–6.14); unadjusted two-proportion z-test p = <0.001.

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.

Percentage of Participants With CO Confirmed 4-Week CA From Smoking

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Varenicline: 37.8% (287/760) versus 12.5% (94/750) on control; risk difference 25.2 percentage points (95% CI 21.0 to 29.4), risk ratio 3.01 (2.44–3.72); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Varenicline than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With CO Confirmed Long Term CA From Smoking

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Varenicline: 27.0% (205/760) versus 9.9% (74/750) on control; risk difference 17.1 percentage points (95% CI 13.3 to 20.9), risk ratio 2.73 (2.14–3.50); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Varenicline than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With 4-Week Point Prevalence of Smoking Cessation

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Varenicline: 32.8% (249/760) versus 17.3% (130/750) on control; risk difference 15.4 percentage points (95% CI 11.1 to 19.7), risk ratio 1.89 (1.57–2.28); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Varenicline than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the posted secondary outcomes, the direction of the arm percentages is consistent with the primary result: each listed endpoint has a higher percentage in the varenicline arm than in the placebo arm. These secondary measures cover a shorter continuous-abstinence interval, a longer follow-up interval, and point-prevalence assessments. Together they provide additional views of smoking cessation at different times and under different definitions. They are related to the primary outcome, but they are not identical replications of it.

In particular, continuous abstinence over an interval requires a sustained pattern meeting the recorded definition, while point prevalence concerns status at a specified assessment. Differences in timing and outcome definition mean that secondary results can add context without being substituted for the primary endpoint. The long-term measure also addresses a later period than the primary assessment, so it speaks to a different aspect of follow-up.

The registry reports individual logistic-regression analyses for the secondary outcomes, and the posted recalculated comparisons have p-values of p < 0.001. The registry record does not report a multiplicity adjustment or a plan controlling the overall false-positive risk across secondary comparisons. When several outcomes are examined, unadjusted p-values do not account for the number of opportunities to observe a nominally notable result. This is why the secondary findings generally carry less inferential weight than a designated primary outcome, particularly when the analysis plan for the family of tests is not reported.

The consistent direction across these outcomes is descriptive context, not proof that all outcomes were independently confirmed or that every measure has the same clinical meaning. The registry record does not report whether the secondary analyses were prespecified in the detailed protocol, how missing data were handled for each measure, or whether any additional multiplicity procedure was used. These limits support treating the secondary results as supportive rather than as separate definitive tests.

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

• Percentage of Participants With CO Confirmed 4-Week CA From Smoking
• Percentage of Participants With CO Confirmed Long Term CA From Smoking
• Percentage of Participants With 7-Day Point Prevalence of Smoking Cessation
• Percentage of Participants With 4-Week Point Prevalence of Smoking Cessation

9. Statistical Interpretation

10. Statistical Methods Explained

The registry record reports a logistic-regression analysis for the primary comparison and labels its effect measure an odds ratio. The posted arm percentages and the simple recalculation are useful alongside that sponsor analysis, but they answer related rather than identical statistical questions. The exact covariates, model specification, and handling of any model assumptions are not reported in the registry record.

What does an odds ratio describe?

General statistical explanation: For a binary outcome, odds compare the chance of an event with the chance of no event. An odds ratio compares those odds between groups. A value of 1 represents equal odds in the groups; values above 1 indicate higher odds in the group in the numerator, and values below 1 indicate lower odds. An odds ratio is not the same as a risk ratio, and it is not a direct difference between percentages. When an outcome is not rare, an odds ratio can look more extreme than the corresponding risk ratio. For this reason, the arm percentages are important for understanding the observed outcome in ordinary terms.

The sponsor-reported odds ratio comes from logistic regression. The registry record does not state which covariates, if any, were included, so it should not be characterized as adjusted for particular baseline characteristics. The recalculated odds ratio is an unadjusted calculation from the posted summary statistics. The reported and recalculated estimates differ, and the record’s discrepancy flag is false; accordingly, the sponsor’s own analysis takes precedence. A simple recalculation is a check based on posted summaries, not a replacement for the trial’s analysis.

What does a confidence interval add?

General statistical explanation: A confidence interval gives a range of values compatible with the observed data and the statistical procedure, under its assumptions. It conveys precision as well as direction. A narrower interval indicates less uncertainty on that measure’s scale than a wider interval, although interval width alone does not establish whether an effect matters clinically. The sponsor’s 95% confidence interval for the primary odds ratio runs from 6.09 to 12.53. Its endpoints are both above the odds-ratio null value of 1. The interval is not a guarantee that the true effect lies within its endpoints, and it does not account for biases or limitations not represented by the fitted model.

How should the p-value be read?

General statistical explanation: A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the analysis assumptions were true. It is not the probability that chance alone produced the result, and it is not a measure of the probability that treatment is effective. The sponsor reports p < 0.001 for the primary logistic-regression analysis. The recalculated unadjusted comparison reports p < 0.001. These results indicate strong statistical evidence against the corresponding no-association null hypotheses under their respective analyses, but neither p-value measures the size or certainty of an individual participant’s outcome.

Why distinguish the reported and recalculated analyses?

The posted summary statistics allow simple unadjusted comparisons, including odds ratios, risk ratios, and risk differences. Those calculations use the displayed event counts and group sizes and do not reproduce a regression model unless its details and inputs are available. The sponsor’s result is the trial’s reported analysis; the recalculation provides a transparent summary-based comparison. Differences can arise from analysis methods and inputs, but the specific reason for the difference is not reported in the registry record. It would therefore be inappropriate to attribute the difference to a particular adjustment or modeling decision.

Why can over-dispersion matter in other outcome types?

General statistical explanation: Over-dispersion occurs when observed variability exceeds what a statistical model assumes. It is relevant to some count outcomes and can make standard errors too small if ignored. The primary endpoint is binary and is reported as a percentage, with a logistic-regression analysis; over-dispersion is not identified as an issue in the registry record. This general concept should not be mistaken for a reported finding about this trial.

11. Confidence Intervals and Precision

The sponsor-reported primary odds ratio is 8.74, with a 95% confidence interval from 6.09 to 12.53. This interval is entirely above the null odds ratio of 1, and the associated p-value is reported as p < 0.001. The interval gives a range of estimates compatible with the reported regression analysis and its assumptions. Its width reflects uncertainty in the odds-ratio estimate; it does not capture every possible source of uncertainty, such as unreported analysis choices or limitations in the registry record.

The recalculated unadjusted odds ratio is 6.347, with a confidence interval from 4.608 to 8.743. This interval is based on posted summary statistics and is not the sponsor’s logistic-regression interval. Since the registry record does not flag a discrepancy, the sponsor’s analysis takes precedence. The two intervals should therefore not be treated as interchangeable estimates from the same procedure.

The percentages in the two arms, 32.1% and 6.9%, help place the odds-ratio result in context. They are observed proportions for the stated endpoint and analysis population, not estimates of every participant’s future outcome. The confidence interval for the sponsor analysis is on the odds-ratio scale, so it does not directly give an interval for either arm’s percentage or for a percentage-point difference. The registry record does not post a confidence interval for the arm percentages themselves. Precision is thus best described by keeping the measure and analysis attached to each interval rather than transferring interval limits from one scale to another.

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 estimates are illustrations based on the observed effect, not the original trial’s design calculations. For these binary outcomes, the figures are participants per arm, rather than total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column means the estimated participants per arm under the stated assumptions for a future study to have an 80% chance of rejecting the null hypothesis if the assumed effect were the true effect. The 90% power column gives the corresponding planning estimate for a 90% chance. These are design targets, not guarantees about a future study’s result. For the primary outcome, planning for the full observed effect gives 38 participants per arm for 80% power and 50 participants per arm for 90% power. Planning for 75% of the observed effect gives 60 and 79 participants per arm, respectively; planning for 50% gives 113 and 151.

The pattern reflects a general planning principle: smaller effects are harder to distinguish from random variation, so they require more participants under otherwise unchanged assumptions. These calculations do not account for design features that are not included in the stated assumptions, such as loss to follow-up, and they should not be read as evidence about the probability that the completed trial was successful. This is not observed power.

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 = 0.069; treatment proportion p₁ = 0.321; average p̄ = 0.195.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5605 = 1.0986.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5315 = 0.4473.
4. n = (1.0986 + 0.4473)² / (0.2517)² = 37.7, rounded up to 38 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 <- 0.0693333333333333                          # control proportion
p1 <- 0.321052631578947                          # 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(1370356)
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 = 38 (80% power), 50 (90% power)
 75% of observed effect: n per arm = 60 (80% power), 79 (90% power)
 50% of observed effect: n per arm = 113 (80% power), 151 (90% power)
power.prop.test: 37.7 
Simulated power at n = 38 per arm: 0.834 (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. Analyses Reported by the Sponsor

The sponsor’s primary analysis is a logistic regression reporting an odds ratio of 8.74, with a 95% confidence interval from 6.09 to 12.53 and p < 0.001. A simple unadjusted recalculation from the posted group summaries gives an odds ratio of 6.347, with a confidence interval from 4.608 to 8.743. The registry record marks the discrepancy as false. Under that record, the sponsor’s own analysis takes precedence.

The recalculation is not a correction to the sponsor’s result. It is a summary-based comparison that does not reproduce the reported regression unless the model and its inputs are known. The registry record does not report enough detail to explain the numerical difference, so no specific cause should be assigned to it. The sponsor’s interval and p-value should be read as the reported inferential result, while the recalculation offers a separate, unadjusted view of the posted group data.

Both analyses point in the same broad direction: the posted primary abstinence percentage is higher in the varenicline arm, and both statistical comparisons reject their respective no-difference null hypotheses at the reported significance levels. Their effect estimates are not identical and should not be merged. The arm percentages remain a direct description of observed proportions, whereas the sponsor’s odds ratio expresses a model-based comparison on the odds scale.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies a primary endpoint and posts secondary outcome results, but the detailed statistical analysis plan is not reported in the registry record. Whether multiplicity was controlled across secondary outcomes, or across any other analyses, is not reported in the registry record. This matters because repeated statistical testing can increase the chance of at least one apparently notable result when all null hypotheses are true. The posted secondary p-values should therefore be interpreted as unadjusted unless a multiplicity procedure is documented; no such procedure is reported in the registry record.

The primary outcome definition specifies a missing-data rule for carbon monoxide: missing CO was imputed as negative, with the registry’s threshold written as CO ≤ 10 ppm. That rule is important because the outcome requires carbon-monoxide confirmation. Treating missing CO measurements as negative assigns them the stated negative classification for this part of the endpoint. The record does not explain the rationale for this choice or provide sensitivity analyses showing how alternative missing-CO assumptions would affect the result.

Handling of missing self-reported smoking status, missing Nicotine Use Inventory information, and missing data for the secondary endpoints is not reported in the registry record. Participant flow, reasons for missing assessments, and any additional imputation procedures are also not reported. The primary efficacy population is described as the Intent-to-Treat population consisting of all randomized participants, but the registry record does not provide sufficient detail to assess how every randomized participant contributed to each endpoint analysis.

Interim analyses, stopping rules, and any adjustment related to repeated looks at the data are not reported in the registry record. The original sample-size justification, prespecified covariates, model diagnostics, and complete analysis plan are likewise not reported. These absences do not establish that the procedures were omitted; they limit what can be concluded from the registry record alone.

16. 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: myocardial infarction (0.3%), ovarian cyst (0.3%), vertigo (0.1%), ileus (0.1%), vomiting (0.1%).

The serious adverse event figures list 28 affected participants among 751 at risk in the varenicline group and 16 among 742 at risk in the placebo group. The figures for other adverse events list 467 among 751 at risk in the varenicline group and 339 among 742 at risk in the placebo group. These are posted counts and denominators, not proof that an event was caused by the assigned intervention. The safety denominators differ from the arm sizes shown for the primary efficacy results, and the registry record does not explain the difference.

The listed serious-event terms include myocardial infarction and ovarian cyst, each reported as 0.3%, and vertigo, ileus, vomiting, and chest pain, each reported as 0.1%. These terms describe events recorded in the registry, not a complete assessment of their clinical context or comparative risk. The registry record does not report death counts. It also does not provide event-level timing, severity detail beyond the serious-event classification, or a causal assessment sufficient to attribute these events to treatment.

Comparisons of safety counts need to account for the population at risk, the way events were collected, and the duration of observation. Those details are not fully reported in the registry record. The posted figures should therefore be read as descriptive safety data, not as a stand-alone determination of comparative safety.

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

The posted results show a higher percentage meeting the primary carbon-monoxide-confirmed continuous-abstinence definition in the varenicline arm than in the placebo arm during Week 15 through Week 24. The sponsor’s logistic-regression analysis reports an odds ratio of 8.74, with a 95% confidence interval from 6.09 to 12.53 and p < 0.001. These statistics describe the trial’s primary comparison under the reported analysis. They do not mean that every person assigned varenicline achieved abstinence or that the same result would occur in every setting.

The result is specific to the enrolled study population, the recorded endpoint definition, the assessment interval, and the handling of missing carbon-monoxide results. It does not by itself establish abstinence outside the measured interval, effects on outcomes not posted in the registry, or effects for people whose circumstances differ from those represented in the trial. It also does not quantify the experience of any individual participant.

Statistical significance is not the same as clinical importance, and an odds ratio is not a direct measure of the absolute difference between groups. The arm percentages help describe the observed outcome, while the odds ratio summarizes the relative odds under the sponsor’s model. Both should be considered with the confidence interval, analysis details, secondary results, and safety information. The registry record does not report all details needed to judge generalizability, missing-data sensitivity, or the full balance of benefits and harms.

The appropriate conclusion is therefore bounded: the posted primary efficacy result favors the varenicline arm on the specific abstinence outcome measured, with strong statistical evidence under the sponsor-reported analysis. The data do not establish that the treatment works for every person, resolve all questions about safety, or remove uncertainty arising from missing or unreported methodological details.

18. Why This Trial Matters Statistically

This trial is statistically informative because its primary outcome combines a defined period of continuous abstinence with carbon-monoxide confirmation. That makes the endpoint more specific than a single report of smoking status at one visit, while still relying partly on participant-reported nicotine use and on the recorded missing-CO rule. The endpoint’s definition is essential to interpreting what the estimated effect does and does not represent.

The comparison also illustrates why effect measures need to be kept distinct. The arm percentages are directly understandable observed proportions, whereas the sponsor reports an odds ratio from logistic regression. A summary-based unadjusted recalculation gives a different odds-ratio estimate, and the registry record does not flag a discrepancy. Treating the sponsor’s analysis as primary while retaining the recalculation as a check makes the distinction between a trial-reported model and a simple summary calculation clear.

The secondary outcomes add information across different abstinence definitions and follow-up periods, but their interpretation depends on multiplicity and missing-data practices. Since those procedures are not fully reported, the secondary results should not be treated as equivalent to the designated primary analysis. The planning estimates also demonstrate how assumptions about the effect to detect shape future-study size requirements; they are planning illustrations, not evidence about the probability of success in the completed trial.

Finally, the safety counts are descriptive and use denominators that differ from those displayed for efficacy. Reading efficacy, uncertainty, missing-data handling, and safety together is necessary for a balanced statistical account. The record supports a clear primary comparison but leaves important methodological details unreported.

19. 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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several trial-specific details that would help assess validity and applicability are not reported in the registry record. These include the randomization procedure and allocation concealment, the method used to maintain double-blinding, the treatment regimen, adherence information, and the nature of any accompanying cessation support. Without these details, the record alone cannot establish how closely the conduct matched the stated design.

The primary endpoint depends on participant reports and clinic carbon-monoxide measurements. The record states that missing CO was imputed as negative, but it does not report sensitivity analyses under alternative assumptions. Handling of missing smoking reports and missing data for the secondary outcomes is not reported. Participant flow, reasons for missing assessments, and the extent of protocol deviations are also not reported in the registry record.

The detailed analysis plan, original sample-size justification, prespecified regression covariates, and model diagnostics are not reported. The sponsor’s logistic-regression estimate differs from the summary-based unadjusted recalculation, but the reason for that difference is not reported. Multiplicity procedures for secondary outcomes and interim-analysis practices are not reported either. These gaps constrain independent assessment of the modeling and the secondary findings.

For safety, the registry reports event counts and denominators, but not enough context about timing, duration of observation, event adjudication, or causal attribution to make the counts a complete comparative safety assessment. Death counts are not reported in the registry record. The multinational setting is stated, but sites, participant characteristics, and subgroup results are not reported in the registry record. These limitations restrict how broadly the posted findings can be applied.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study To Evaluate The Efficacy And Safety Of Varenicline Compared To Placebo For Smoking Cessation Through Reduction — NCT01370356.
• Registry record last updated 2014-09-01; status last verified 2014-08.
• Results first posted 2014-09-01.
• 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.

23. Record Summary

The registry record describes a completed, multinational, randomized, double-blind, parallel-group Phase 4 comparison of varenicline with placebo for smoking cessation through reduction. Enrollment was 1510. The primary endpoint was carbon-monoxide-confirmed continuous abstinence during Week 15 through Week 24 in the Intent-to-Treat population.

The posted primary abstinence percentages were 32.1% for varenicline and 6.9% for placebo. The sponsor-reported logistic-regression odds ratio was 8.74, with a 95% confidence interval from 6.09 to 12.53 and p < 0.001. The registry record does not report the complete analysis plan, original sample-size justification, multiplicity procedures, or several details about missing data and trial conduct. Safety results are posted as event counts and denominators, with deaths not reported in the registry record.