An Alternative Dosing Schedule of Varenicline for Smoking Cessation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for An Alternative Dosing Schedule of Varenicline for Smoking Cessation (NCT00835900), a randomized phase 2 study. The primary outcome is Change in Smoking Behavior.

2. Clinical Question

The study’s broader stated purpose was to explore whether a prolonged alternative varenicline schedule could be associated with greater quit rates and higher rates of continuous abstinence. The posted primary outcome, however, is specifically change in cigarettes per day over the stated Week 2 to Week 5 interval. It is not itself a direct measure of continuous abstinence or a complete summary of smoking cessation over a longer period.

The secondary outcome concerns rates of smoking cessation 12 weeks after the quit date. That outcome complements the primary measure by addressing cessation at a later time point, but it is a separate endpoint and should be read on its own terms. The registry record does not report a detailed definition of cessation, the quit-date procedures, or additional outcome-assessment details.

The central statistical question is whether the observed group difference in cigarette-use change is sufficiently precise to distinguish it from no difference, and how that result sits alongside the secondary cessation outcome. The posted results are estimates from a small pilot study, so their uncertainty and the limits of the registry information matter when interpreting the pattern.

3. Trial Design

This was a phase 2, randomized, triple-masked, parallel-group study. The registry reports enrollment of 60 participants and a completed status. The study is titled “An Alternative Dosing Schedule of Varenicline for Smoking Cessation”; its official title is “Extended Varenicline for Smoking Cessation: A Pilot Study.” Roswell Park Cancer Institute is listed as the sponsor. The recorded start was 2009-03, and primary completion was 2010-07.

Participants were assigned to the Extended Run-In or Standard Run-In arm. The registry describes the varenicline intervention as drug plus counseling and the placebo intervention as placebo plus counseling. The arm names and the intervention descriptions are not identical labels; the record does not provide enough detail to reconstruct the exact dosing schedules or their timing. The stated purpose was to explore an extended alternative schedule, but the protocol-level description is not reported in the registry record.

Randomization means that assignment was intended to use a chance-based process, rather than being selected by the participant or investigator. Triple masking indicates that the registry classifies the study as masked at three levels, but it does not identify those parties or provide details of how masking was implemented. A parallel design means the groups are compared across separate arms rather than through a crossover in which participants receive both regimens.

The primary outcome was change in cigarettes per day from Week 2 to Week 5, in the ITT population. The registry reports means and standard errors for each arm. It also lists a secondary outcome, participants who achieved smoking cessation 12 weeks after the quit date. The posted record has no reported analyses listed for that secondary outcome, despite posting outcome counts and an unadjusted comparison.

Further design information—including eligibility criteria, the precise intervention schedules, the original sample-size rationale, and the planned statistical analysis—is not reported in the registry record. The total enrollment and the posted arm counts describe the trial record, but do not by themselves explain how the original design decisions were made.

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

Analysis population for the primary outcome, as defined in the registry: ITT

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 Change in Smoking Behavior, measured over Change in cigarettes per day from Week 2 to Week 5.

The primary endpoint measures change in the number of cigarettes smoked per day between Week 2 and Week 5. It is a continuous measure: each participant’s change can take a range of values, rather than being limited to an event/no-event classification. The registry states that the measure is analyzed as a mean and identifies the population as ITT.

A change score focuses on how smoking behavior shifted across the specified interval. In this trial, the group means are negative, indicating a reduction in cigarettes per day over that interval as the endpoint is recorded. The group mean summarizes the average change, while the standard error describes uncertainty around the estimated group mean. Neither is a description of every individual participant’s experience.

Comparing the average change between randomized groups addresses whether the observed amount of change differed between the assigned strategies. This continuous endpoint can capture differences in smoking behavior that a binary quit/not-quit outcome would not represent. It also does not, by itself, establish sustained abstinence or describe smoking behavior outside the stated interval.

The registry provides the Week 2 to Week 5 timeframe and the unit, but does not report further details about measurement procedures, handling of missing observations, or the clinical interpretation assigned to different magnitudes of change. Those details are relevant to a full assessment of how the endpoint was collected and analyzed.

7. Results Posted in the Registry

• Extended Run-In: mean -6.30 versus -3.20 on control; difference -3.10 (95% CI -5.33 to -0.87), standardized effect d = -0.69; z-test p = 0.007.

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.

Rates of 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:
  • Extended Run-In: 53.1% (17/32) versus 39.3% (11/28) on control; risk difference 13.8 percentage points (95% CI -11.2 to 38.9), risk ratio 1.35 (0.77–2.38); unadjusted two-proportion z-test p = 0.284.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Extended Run-In and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcome concerns smoking cessation 12 weeks after the quit date. Its group comparison is less statistically conclusive than the primary comparison: the risk-difference interval includes no difference, and the unadjusted p-value is 0.284. This means the posted secondary data do not sharply distinguish among a range of possible group contrasts. It does not demonstrate that the groups are equivalent or that no difference exists.

The primary outcome and this secondary outcome are related through the broader subject of smoking behavior, but they do not measure the same thing. One describes average cigarette-per-day change over Week 2 to Week 5; the other records cessation at a later specified time. A difference in the first outcome need not translate into a similarly precise result for the second. The secondary finding therefore neither directly confirms nor negates the primary result.

Unadjusted secondary comparisons generally carry less weight in an overall interpretation than a clearly prespecified primary comparison, particularly when the registry does not document a multiplicity strategy. When several outcomes are examined, the opportunity for an apparently notable result can increase. Adjustments or a prespecified hierarchy may help control interpretation, but neither is reported in the registry record. The secondary result should therefore be treated as supporting context rather than as a stand-alone definitive conclusion.

The registry lists one secondary outcome and posts its counts and comparison, while reporting no analyses in the reported-analyses listing. The record does not state whether the secondary analysis was planned in advance, whether other outcomes were examined, or how missing observations were handled. Those unknowns limit the strength of any broader inference drawn from the secondary outcome.

Across the endpoints, the main statistical pattern is that the primary continuous measure shows a group contrast whose posted confidence interval is on one side of zero, while the binary secondary comparison remains uncertain. This contrast is useful for understanding the evidence structure, but the outcomes should remain distinct. It would be inappropriate to treat the secondary result as a replication of the primary measure or to combine the two into an unreported overall effect.

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

• Rates of Smoking Cessation.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, so the registry reports a mean change for each arm and a standard error for each mean. A mean gives a concise description of the center of the observed changes. The standard error describes the sampling uncertainty of that estimated mean: in general, it is not the same as the spread of individual participant values. Individual changes may vary more widely than the standard error suggests.

What does the mean difference represent?

The posted comparison is a mean difference between the Extended Run-In and Standard Run-In groups. Its value is -3.1 cigarettes per day. The comparison is oriented as the Extended Run-In group relative to the Standard Run-In group. A negative difference therefore corresponds to a more negative mean change in the Extended Run-In group, consistent with a greater average reduction over the measured interval in these posted results.

A group difference is an estimate, not a direct observation that every participant in one group changed by that amount more than every participant in the other. It summarizes the contrast between group averages. General statistical interpretation also depends on how the groups were assigned, how outcomes were measured, and how missing observations were handled. Randomization is reported, but the missing-data procedures and measurement details are not reported in the registry record.

How should a confidence interval be understood?

In general, a confidence interval expresses the uncertainty around an estimated quantity using a method with a specified long-run coverage property. It shows a set of values reasonably compatible with the observed data and the method’s assumptions. It is not a range containing a known proportion of individual participants’ outcomes, and it is not a guarantee about the result of a future study.

For the primary mean difference, the posted interval runs from -5.335 to -0.865. Because both limits are negative, the interval is consistent with a greater average decline in the Extended Run-In group for this outcome. The interval also makes clear that the exact size of the group difference is uncertain. Statistical significance, where assessed through a test, does not remove that uncertainty or establish clinical importance.

What does the p-value add?

A p-value describes how unusual data at least as inconsistent with a specified null model would be, if that model and the test assumptions were true. It is not the probability that the null hypothesis is true, nor the probability that the result happened “by chance.” The primary unadjusted p-value is 0.007. It is a summary of evidence against a no-difference null model under the test used; the registry record does not report the full test specification.

The secondary unadjusted p-value is 0.284. For that outcome, the posted confidence interval includes no difference. A p-value and confidence interval are related summaries, but neither supplies information about unreported analysis choices, data quality, or the appropriateness of the endpoint.

Why distinguish outcome types?

The primary outcome is continuous, while the secondary cessation outcome is binary in the posted results: participants are counted according to whether they are recorded as having cessation. A mean difference is a natural summary for a continuous outcome. A risk difference compares the proportion of participants with an event between groups, and is expressed as an absolute difference between those proportions. The secondary comparison is reported as a risk difference, with an estimate of 0.138. Its confidence interval ranges from -0.112 to 0.389.

Different measures answer different questions. The continuous result describes mean change in cigarettes per day; the risk difference describes an absolute contrast in the recorded cessation outcome. These measures should not be treated as interchangeable, and their estimates should not be compared as if they were expressed on the same scale.

What does unadjusted mean?

An unadjusted comparison is reported without a statistical correction for the other comparisons or factors that might be considered in a broader analysis. General statistical practice distinguishes a single test from a family of tests: when many outcomes or comparisons are examined, the chance of at least one apparently unusual result can increase. Adjustment procedures can address that issue, but the registry does not report whether any were planned or performed. The posted p-values are therefore best described as unadjusted.

The record lists two outcome measures and one posted secondary outcome, but it reports zero analyses in its analyses listing and an empty list of reported secondary analyses. This is a registry reporting limitation: it does not establish which analysis decisions were made outside the posted record. The sponsor’s own analysis is not identified as conflicting with the recalculated comparison; the discrepancy indicator is false.

Why can over-dispersion matter?

As a general statistical concept, over-dispersion occurs when observed variability is greater than a model assumes. It can make standard errors too small if the model does not account for the extra variation, leading to intervals that are too narrow and tests that appear more decisive than warranted. The primary result is summarized with standard errors, but the registry does not report an over-dispersion assessment or a model specification. It would therefore be inappropriate to infer that over-dispersion was assessed or that a particular correction was used.

For a binary outcome, the precision of a risk-difference estimate depends on the number of participants and on the observed event frequencies. General methods may use approximations that behave differently with small samples or sparse events. The registry record does not identify the method used for its secondary comparison. The posted estimate and interval can be described, while the exact calculation method remains unreported.

Finally, statistical results are conditional on the population, endpoint definitions, and analysis methods used. The ITT label is given for the primary endpoint, but further details of the analysis population and handling of departures from assigned treatment are not reported in the registry record. Those omissions limit how fully the published summaries can be audited from the registry alone.

11. Confidence Intervals and Precision

The primary mean difference is -3.1 cigarettes per day, with a confidence interval from -5.335 to -0.865. The interval lies below zero, which is consistent with a more negative mean change in the Extended Run-In group than in the Standard Run-In group. Its width reflects meaningful uncertainty about the precise magnitude of that contrast. The data support a range of possible differences rather than one exact value.

The arm-level means are -6.3 and -3.2, with standard errors of 0.9 and 0.7, respectively. Standard errors quantify uncertainty in the estimated means; they do not show the full range of individual participant changes. The registry does not post arm-level confidence intervals for these means.

The secondary risk-difference interval runs from -0.112 to 0.389 around an estimate of 0.138. It includes zero and spans both negative and positive values, so the posted results leave substantial uncertainty about the direction and size of the cessation contrast. The event counts are modest, and the registry does not report a separate precision analysis or the method used to form this interval.

In general, a confidence interval is most informative when read alongside its estimate, endpoint, and assumptions. An interval that excludes zero may be statistically distinguishable from no difference under the stated method, but it does not establish importance or eliminate uncertainty. An interval that includes zero does not prove that groups are equivalent; it indicates that the data are compatible with no difference as well as with other values inside the interval. The registry does not report a prespecified equivalence margin for either outcome.

The primary estimate is more statistically distinct from zero than the secondary estimate in the posted comparisons, but the endpoints differ in type and timeframe. The evidence should not be compressed into a single conclusion about smoking cessation. The precision of each estimate and the scope of its endpoint both matter.

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 sample-size display is a planning illustration based on fractions of the effect observed in this study. The figures are participants per arm, not total participants, because the outcomes are not time-to-event outcomes. The registry’s stated 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 defined as the stated fraction of the observed effect.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect and the assumptions were correct. The 90% column uses a higher target chance of detection and therefore generally calls for more participants per arm. These power levels describe a prospective design calculation; this is not observed power.

For the primary outcome, planning for 100% of the observed effect gives 34 participants per arm for 80% power and 45 for 90% power. Planning for 75% of the observed effect gives 59 and 79 participants per arm, respectively. Planning for 50% of the observed effect gives 133 and 178 participants per arm. The secondary outcome has its own planning figures, based on its observed effect: 203 and 271 participants per arm at 100%, 359 and 480 at 75%, and 802 and 1,073 at 50%, for the respective power targets.

The pattern reflects a general design principle: smaller effects are harder to distinguish from random variation, so more participants are needed to detect them at the same power target. These calculations are illustrations based on the observed estimates, not the trial’s original design justification. The trial’s own sample-size assumptions and justification are not reported in the registry record. The displayed planning figures should not be interpreted as proof that the completed trial did or did not have adequate 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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -3.100; pooled standard deviation σ = 4.499.
2. n = 2 × (1.96 + 0.842)² × 4.499² / -3.100² = 33.1, rounded up to 34 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
delta <- -3.1                      # observed difference in means
sigma <- 4.49896539830797                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(835900)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 34 (80% power), 45 (90% power)
 75% of observed effect: n per arm = 59 (80% power), 79 (90% power)
 50% of observed effect: n per arm = 133 (80% power), 178 (90% power)
power.t.test: 34.1 
Simulated power at n = 34 per arm: 0.797 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 does not report a multiplicity plan. It does not state whether the primary outcome was the sole confirmatory test, whether secondary outcomes were treated as exploratory, or whether any statistical adjustment was used for the number of outcomes or comparisons. The posted p-values are unadjusted. Without a documented plan, they should not be interpreted as multiplicity-adjusted evidence across the full set of possible analyses.

Multiplicity is a general concern when researchers test several hypotheses: even if no true differences exist, repeated testing can increase the chance of obtaining at least one result that appears unusual. A prespecified testing hierarchy, adjustment, or clear exploratory framing can help readers understand that risk. None of those procedures is reported in the registry record, so no particular approach should be assumed.

The registry identifies the primary population as ITT, but does not describe how the population was operationalized. It does not report how participants with missing outcome data were handled, whether all randomized participants contributed to each analysis, or whether any sensitivity analyses were conducted. Missing-data methods can affect estimates and uncertainty, especially if missingness differs between groups or relates to outcomes. The posted summaries alone do not resolve those questions.

For the secondary endpoint, the registry lists no reported analyses, despite posting an outcome comparison. This limits the ability to determine whether the displayed comparison reflects the planned method or whether other analyses were undertaken. The details of allocation concealment, adherence, protocol deviations, and the identities of those masked are also not reported in the registry record.

These omissions do not establish that the trial lacked a statistical plan or that particular procedures were not performed. They mean only that those details cannot be confirmed from the registry record. Interpretation should therefore distinguish the results that are posted from the analysis decisions and data-handling practices that remain undocumented.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: irritability (3.6%).

The registry reports serious adverse events for the two arms using counts of affected participants and participants at risk. In the Extended Run-In group, 0 of 32 participants were recorded as affected by a serious adverse event. In the Standard Run-In group, 1 of 28 was recorded as affected. The record lists zero deaths in each group.

These figures are counts from this study, not estimates of the full range of possible risks. With enrollment of 60, uncommon events may not be well characterized, and a zero count does not establish that an event cannot occur. The registry also lists other adverse events affecting 18 of 32 participants in the Extended Run-In group and 6 of 28 in the Standard Run-In group. These are presented separately from the serious-event counts and should not be conflated with them.

Irritability is listed as a serious-event term with a reported value of 3.6%. The record does not provide further detail about the term’s attribution or context. The adverse-event summaries do not establish causation, and the registry does not report additional information about event severity, timing, relatedness assessments, or statistical comparisons. These figures describe the recorded events in the registry, rather than providing a complete safety assessment.

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

The posted primary data show a more negative mean change in cigarettes per day in the Extended Run-In arm than in the Standard Run-In arm over Week 2 to Week 5. The estimated mean difference is -3.1, and its confidence interval is entirely below zero. This is a statistical contrast in the stated continuous outcome and timeframe. It is not a direct estimate of sustained abstinence, nor does it establish that every participant experienced a reduction.

The secondary cessation comparison is less precise. Its interval includes no difference and extends to values on either side, so the posted result leaves considerable uncertainty about the size and direction of the group contrast. The primary and secondary findings address different endpoints and should not be treated as contradictory or combined into an unreported overall measure.

The study is described as a pilot, and enrollment was 60. The registry’s planning illustrations show that larger samples would be needed to detect smaller fractions of the observed effects under the stated assumptions. Those illustrations do not report the original design rationale and are not evidence of the trial’s observed power. They help describe why estimates from a small study may remain uncertain, especially for participant-count outcomes.

These results do not prove a causal explanation beyond the randomized comparison as recorded, establish a benefit for an individual, or determine whether the strategy is appropriate for any particular person. They also do not answer questions about outcomes outside the posted timeframes, detailed adherence, or longer-term abstinence. Medical decisions require individual clinical judgment and evidence beyond this registry summary.

The registry record does not report enough methodological detail to fully evaluate missing data, the planned analysis, multiplicity handling, or the exact schedules used in the arms. The results are therefore best read as the posted estimates and their uncertainty, with the unreported design and analysis details kept in view.

17. Why This Trial Matters Statistically

This study illustrates why endpoint definition matters. A continuous change in cigarettes per day and a binary cessation outcome may both concern smoking behavior, but they answer different statistical questions. Their estimates have different scales and timeframes, so one cannot stand in for the other. The primary result is more distinct from zero in the posted comparison, while the secondary outcome remains imprecise.

It also demonstrates the value of reading estimates alongside their uncertainty. A point estimate alone can make a contrast seem more definite than it is. The primary confidence interval indicates a range of plausible values for the mean difference, while the wider secondary uncertainty cautions against treating the observed cessation contrast as settled. Statistical significance is not a substitute for considering precision or endpoint relevance.

The planning illustrations make another important point: power calculations depend on the effect size a study is intended to detect. Smaller effects require more participants under otherwise comparable assumptions. The illustrations are based on observed effects and are not the original design justification, so they should be read as planning scenarios rather than as an evaluation of the trial’s performance.

Finally, registry completeness affects how results can be assessed. The record identifies randomization, masking, the parallel design, and an ITT label for the primary outcome, but leaves important analytic and data-handling details unreported. Clear reporting of those details would help readers distinguish prespecified analyses from exploratory ones and evaluate the possible impact of missing data and multiple comparisons. This case shows that numerical results are most useful when paired with transparent methods.

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.

This registry record gives limited detail about eligibility criteria, participant characteristics, and the exact varenicline and placebo schedules. Although the study aim refers to a prolonged alternative schedule, the dose, duration, and schedule differences are not reported in the registry record. It is therefore not possible to reconstruct the full treatment contrast from the posted description.

The primary endpoint covers change from Week 2 to Week 5, while the secondary cessation endpoint is measured 12 weeks after the quit date. The record does not report additional follow-up outcomes or explain how the two timeframes were selected. The cessation definition and assessment procedures are also not reported, which limits assessment of how the outcome was classified.

The registry identifies the primary population as ITT but does not describe exclusions, missing-data handling, treatment adherence, or protocol deviations. It also does not report the statistical analysis plan, covariate adjustment, or multiplicity procedures. The record lists no reported analyses for the secondary outcome, despite posting a comparison, leaving its analysis status unclear.

Enrollment of 60 limits the amount of information available, particularly for event counts and less common safety outcomes. The serious adverse-event figures are sparse, and zero recorded deaths does not establish the absence of risk. The record does not include details about event timing, relatedness, or follow-up completeness.

Finally, the registry does not report the original sample-size justification or design assumptions. The planning illustrations are based on observed effects and cannot fill that gap. These limitations do not invalidate the posted estimates, but they constrain how fully the study’s design, analysis, and generalizability can be evaluated from the registry record alone.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: An Alternative Dosing Schedule of Varenicline for Smoking Cessation — NCT00835900.
• Registry record last updated 2017-05-30; status last verified 2017-04.
• Results first posted 2017-05-30.
• 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 describes a completed, randomized, triple-masked, parallel-group phase 2 pilot study sponsored by Roswell Park Cancer Institute, with enrollment of 60. The recorded start was 2009-03 and primary completion was 2010-07. The arms are labeled Extended Run-In and Standard Run-In, with the interventions described as varenicline plus counseling and placebo plus counseling.

The primary endpoint was ITT mean change in cigarettes per day from Week 2 to Week 5. The posted mean difference was -3.1, with a confidence interval from -5.335 to -0.865 and an unadjusted p-value of 0.007. The secondary cessation outcome was recorded 12 weeks after the quit date; its comparison was less precise and its unadjusted p-value was 0.284.

The registry does not report the original sample-size rationale, full statistical plan, or important details of missing-data handling and intervention schedules. The estimates should be interpreted with those reporting limits in mind.