Varenicline and Motivational Advice for Smokers With Substance Use Disorders: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Varenicline and Motivational Advice for Smokers With Substance Use Disorders (NCT00756275), a randomized na study. The primary outcome is 7-day Point-prevalence Smoking Abstinence.

2. Clinical Question

The clinical question is about a measured smoking-cessation outcome at follow-up, not about long-term abstinence. A participant counted as abstinent had to meet the registry’s 7-day smoking-cessation definition and biochemical confirmation criteria. The analysis population was described as intent to treat, with people who were lost counted as smoked. This rule makes loss to follow-up count against abstinence for the primary outcome, although the registry record does not give further detail about follow-up completion or missing-data handling for other outcomes.

The comparison concerns the assigned medication regimens within a behavioral support context. The record describes counseling and related support as part of the intervention, but does not report enough detail to characterize the counseling dose, adherence, or whether its delivery differed by arm. The registry also does not report the original sample-size justification or the full statistical analysis plan. The result therefore addresses the registered outcome and comparison, while questions about implementation and design rationale remain unanswered in the registry record.

3. Trial Design

This was a randomized, parallel-group trial with quadruple masking. The registry lists the phase as NA and the study status as completed. Enrollment was 158. Brown University is listed as the sponsor. The recorded study start was 2009-01, and primary completion was 2014-03.

The registered comparison was between nicotine replacement treatment and varenicline. In the nicotine-replacement arm, participants received a nicotine replacement patch plus a matched placebo pill. In the varenicline arm, participants received varenicline plus matched placebo patches containing no nicotine. The study summary also describes brief advice adapted for sobriety settings, skills training, and medication management. The registry does not report the allocation ratio or further details of the masking procedures.

The primary outcome was assessed at the 3 month follow up. The analysis population was labeled intent to treat, and the registry states that people who were lost were counted as smoked for this endpoint. The arm counts available for the primary result were 60 for nicotine replacement and 77 for varenicline. The registry does not explain the relationship between those outcome counts and total enrollment, or report a participant flow account in the material summarized in the record.

Ten outcome measures and ten analyses are listed in the registry record, and eight secondary outcomes are posted. The secondary outcomes include continuous abstinence duration, smoking days, relapse to drug use, relapse to heavy drinking, and depressive symptoms. The available posted results cover only some of those outcomes. The registry does not report the original sample-size justification, planned interim analyses, or sufficient detail to reconstruct the full statistical plan. These omissions limit evaluation of whether the registered analyses followed a prespecified plan.

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: Five individuals enrolled were found to not meet study criteria, 3 did not pass the medical screen, and 13 individuals were lost prior to being randomized.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: "Intent to Treat" Note: People who were lost were counted as smoked

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 7-day Point-prevalence Smoking Abstinence, measured over 3 month follow up.

The primary endpoint was 7-day point-prevalence smoking abstinence at the 3 month follow up. It counts participants who met the registry’s definition of not smoking during the preceding 7-day period, with cessation confirmed by expired alveolar CO levels of < 10 ppm or salivary cotinine < 16 ng/ml. The result is reported as a number of participants in each group. For the intent-to-treat analysis, people who were lost were counted as smoked.

Point-prevalence abstinence is a snapshot of smoking status during a defined period before assessment. It differs from continuous abstinence, which requires abstinence across a longer interval. The endpoint is useful for comparing the groups at a specified follow-up while applying biochemical confirmation rather than relying solely on self-report. That confirmation helps define the outcome consistently, but the endpoint does not itself describe how long participants remained abstinent outside the 7-day window.

The registry also reports continuous abstinence duration as a secondary outcome, which addresses a different aspect of smoking behavior. Neither measure alone describes every dimension of cessation, such as smoking patterns at other times or long-term status beyond the recorded follow-up. The primary endpoint should therefore be interpreted as a specific, time-limited measure of confirmed abstinence, using the missing-participant rule stated in the registry record.

7. Results Posted in the Registry

• Varenicline + PLA Patch: 13.0% (10/77) versus 3.3% (2/60) on control; risk difference 9.7 percentage points (95% CI 0.9 to 18.4), risk ratio 3.90 (0.89–17.12); unadjusted two-proportion z-test p = 0.047.

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.

Length of Longest Continuous Abstinence

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Varenicline + PLA Patch: mean 7.84 versus 6.25 on control; difference 1.59 (95% CI -2.01 to 5.19), standardized effect d = 0.15; z-test p = 0.387.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Varenicline + PLA Patch and the control. The interval gives the range of effects that remain compatible with the data.

Percent Smoking Days

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Varenicline + PLA Patch: mean 70.37 versus 62.39 on control; difference 7.98 (95% CI -8.38 to 24.34), standardized effect d = 0.21; z-test p = 0.339.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Varenicline + PLA Patch and the control. The interval gives the range of effects that remain compatible with the data.

Percent Relapsed to Drug Use

• 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 + PLA Patch: 13.5% (7/52) versus 10.8% (4/37) on control; risk difference 2.7 percentage points (95% CI -11.0 to 16.3), risk ratio 1.25 (0.39–3.95); unadjusted two-proportion z-test p = 0.708.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Varenicline + PLA Patch and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address related but distinct aspects of smoking and substance-use outcomes. Across the available comparisons, the posted estimates do not provide a consistent body of precise evidence that resolves the primary result. Some point estimates differ between groups, but the reported and recalculated uncertainty is substantial. The continuous secondary comparisons have intervals that include no mean difference, and the relapse-to-drug-use comparison is also imprecise.

These outcomes can add context to the primary abstinence measure: duration of abstinence and smoking days describe other dimensions of smoking behavior, while relapse outcomes concern substance use and heavy drinking. They do not directly replicate the primary endpoint, which is confirmed 7-day smoking abstinence at the 3 month follow up. Accordingly, the secondary pattern neither establishes nor overturns the primary comparison.

Unadjusted secondary results generally carry less weight than a prespecified primary analysis. When multiple outcomes are tested, the chance of at least one apparently unusual result can increase unless the analysis plan addresses multiplicity. The registry record does not report a multiplicity adjustment or a hierarchy for secondary testing. The outcomes should therefore be treated as exploratory or contextual unless the analysis plan establishes otherwise; that plan is not reported in the registry record.

The registry lists eight posted secondary outcomes, but the detailed results available for interpretation cover only a subset. The record does not explain why outcome counts differ across analyses or whether the unreported outcomes were collected, analyzed, or omitted from posting. No conclusion should be extended to secondary outcomes for which results are not reported in the registry record.

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

• Length of Longest Continuous Abstinence
• Percent Smoking Days
• Percent Smoking Days
• Percent Relapsed to Drug Use
• Percent Relapsed to Drug Use
• Percent Relapsed to Any Heavy Drinking
• Percent Relapsed to Any Heavy Drinking
• Beck Depression Inventory

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant is classified as abstinent or not abstinent under the registry’s definition. A risk difference expresses the difference between the groups’ proportions with the event, in the same units as a proportion. A value above zero in the stated comparison direction means a higher observed abstinence proportion in the varenicline group. The recalculated risk difference is 0.097. Its confidence interval runs from 0.009 to 0.184.

What does the confidence interval describe?

In general, a confidence interval gives a range of effect values compatible with the data and the method used to calculate the interval. It is not a guarantee that the true effect lies within the particular interval, nor does it show the probability that a treatment effect has a particular value. For a risk difference, zero represents no difference between groups. For an odds ratio, 1 represents no difference in odds. Those null values differ because the effect measures use different scales.

The registry reports the sponsor’s primary result as an odds ratio of 4.33, with a 95% confidence interval from .91 to 20.56. The interval includes 1. The recalculated analysis uses a risk difference and gives an interval that does not include zero. These results cannot be compared by simply looking at the numerical size of the estimates: risk differences and odds ratios describe contrasts on different scales. In this case, the record also flags a discrepancy between the sponsor’s analysis and recalculations. The sponsor’s own analysis takes precedence, and the registry does not explain why the reported p-value and confidence interval do not appear to align.

Why use an unadjusted comparison?

An unadjusted comparison summarizes the observed group contrast without controlling for other variables. It can be useful as a transparent description of the posted summary data. It is not necessarily the same as a prespecified adjusted model or the sponsor’s analysis. The registry record does not provide enough information to identify all model details behind the sponsor’s result. The recalculated p-values and intervals should therefore be understood as simple unadjusted re-calculations, not as replacements for the reported trial analysis.

How should the binary outcome be read?

For a binary outcome, the event count and the number assessed matter together. The primary counts are 2 of 60 for nicotine replacement and 10 of 77 for varenicline. A ratio measure such as an odds ratio compares the odds of the event between groups; a difference measure compares the observed proportions directly. With relatively few recorded events, estimates can be sensitive to small changes in counts, and confidence intervals can be wide. This is a general property of sparse binary outcomes, not a claim that any unreported data changed the result.

What do the continuous-outcome methods add?

For continuous outcomes, the registry reports group means and standard deviations. A mean difference estimates the difference in average outcome values between groups. The recalculated mean-difference intervals for the posted continuous outcomes include zero, the value corresponding to no mean difference. The posted continuous comparisons use different outcome scales, so their numerical estimates should not be compared directly with the risk difference for abstinence.

Standard deviation describes variation among participant-level values around a group mean. It is distinct from the standard error, which describes uncertainty in an estimated mean. General statistical practice uses the standard error to quantify the sampling uncertainty of a mean or contrast. The registry does not report participant-level data, so the recalculations use the posted summary statistics rather than a model fitted to individual records.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variation exceeds what a statistical model assumes. If a model assumes less variability than the data contain, standard errors may be too small and confidence intervals too narrow. Appropriate modeling may need to account for the extra variability. The registry record does not report an over-dispersion assessment or enough modeling detail to say whether it was relevant to the sponsor’s analyses. It should therefore be treated as a general consideration, not as a diagnosed feature of this trial.

The posted primary analysis is described as a chi-squared analysis with an odds ratio, and the continuous secondary analyses are described as two-sided t-tests. The registry’s sparse description does not establish every implementation choice, such as handling of covariates or adjustments for multiple comparisons. A method label is useful context, but it does not replace a complete statistical analysis plan.

11. Confidence Intervals and Precision

Precision concerns how tightly an estimate is determined by the data and analysis method. A narrow confidence interval indicates less statistical uncertainty than a wide interval, while a wide interval leaves more plausible values compatible with the observed data. Precision is not the same as clinical importance, and an interval alone does not resolve questions about bias, missingness, or the appropriateness of the analysis.

For the sponsor-reported primary odds ratio, the 95% confidence interval extends from .91 to 20.56 around an estimate of 4.33. The interval is wide and includes the null odds ratio of 1. This means that the reported estimate is not precise enough to exclude a null-compatible value by its confidence interval. The posted p-value is p <0.05, which appears inconsistent with that interval under usual two-sided inference; the registry does not explain the mismatch.

The recalculated primary risk-difference interval is 0.009 to 0.184. It is also broad, although it lies above zero. Since the record flags a discrepancy, the sponsor’s analysis takes precedence. The distinct effect measures and the inconsistency in the posted sponsor statistics both matter when judging precision; the recalculation should not be used to erase the uncertainty in the registry report.

For secondary outcomes, the intervals are also broad relative to their point estimates. The confidence intervals for continuous outcomes include zero, and the binary relapse comparison includes no difference. This is consistent with limited precision, not proof that the groups are identical. The registry record does not report enough information to determine whether missing secondary assessments further affected precision. Overall, the available estimates leave uncertainty about the size and direction of several contrasts.

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 figures are planning illustrations based on the observed effects, not the trial’s original design calculations. For the non-time-to-event outcomes in this record, the values are participants per arm. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each scenario targets the stated fraction of the observed effect. The sample-size assumptions for the trial’s original design are not reported in the registry record.

The columns for 80% and 90% power describe the number of participants per arm estimated to be needed, under those assumptions, to have the corresponding chance of detecting the specified effect if that effect were the true one. They are not probabilities that the observed trial result is correct. The 90% power planning target requires more participants per arm than the 80% target for the same assumed effect. The sample-size curve offers a visual reading of how the planning estimates vary across effect assumptions; it does not add evidence about what the trial observed.

The rows plan for 100%, 75%, or 50% of the observed effect. A smaller assumed effect is harder to distinguish from random variation, so the planning estimates require more participants per arm. These figures are conditional illustrations, not a claim that the trial could or should have enrolled a particular number. They do not account for unreported design choices or establish the adequacy of the original study size. 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 = 0.033; treatment proportion p₁ = 0.130; average p̄ = 0.082.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3872 = 0.7588.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3811 = 0.3207.
4. n = (0.7588 + 0.3207)² / (0.0965)² = 125.1, rounded up to 126 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 <- 0.0333333333333333                          # control proportion
p1 <- 0.12987012987013                          # 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(756275)
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 = 126 (80% power), 167 (90% power)
 75% of observed effect: n per arm = 193 (80% power), 258 (90% power)
 50% of observed effect: n per arm = 364 (80% power), 487 (90% power)
power.prop.test: 125.1 
Simulated power at n = 126 per arm: 0.830 (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 own primary analysis reports an odds ratio of 4.33, a 95% confidence interval from .91 to 20.56, and p <0.05, using a chi-squared method. The simple unadjusted recalculation reports a risk difference of 0.097, with a 95% confidence interval from 0.009 to 0.184 and p = 0.047. The two analyses use different effect measures, and the record flags a discrepancy. The sponsor’s own analysis takes precedence over the recalculation.

The primary sponsor result has an apparent internal tension: its confidence interval includes the null odds ratio of 1, while its reported p-value is below 0.05. The registry record does not explain the difference. The recalculation’s interval and p-value do not remove that uncertainty, because they are based on a simple unadjusted approach and a different measure.

Similar differences appear in posted secondary results. For longest continuous abstinence, the sponsor reports a mean difference of -1.59 and p = .50, while the recalculated contrast is expressed in the opposite comparison direction and has p = 0.387. For percent smoking days, the sponsor reports -7.98 and p = .34; the recalculation gives p = 0.339. For relapse to drug use, the sponsor reports p = .57, while the recalculated p-value is 0.708. These figures should be read as separate reported and recalculated analyses, not blended into a single result. The registry does not provide enough detail to resolve the differences.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when an analysis evaluates multiple outcomes, comparisons, or time points. In general, repeated testing can increase the chance of observing at least one result that appears noteworthy by chance. Common approaches include prespecifying a primary outcome, using a testing hierarchy, or adjusting statistical thresholds. The registry record identifies a primary outcome and lists secondary outcomes, but a multiplicity strategy is not reported in the registry record.

The record lists ten outcome measures and ten analyses, while eight secondary outcomes are posted. It does not report planned interim analyses, a complete statistical analysis plan, or the original sample-size justification. These details matter because they help distinguish confirmatory analyses from exploratory ones and clarify which results were selected for emphasis. Their absence from the registry record does not prove that such plans did not exist; it means they are not reported in the registry record.

For the primary outcome, the stated intent-to-treat population includes a specific missing-participant rule: people who were lost were counted as smoked. This rule assigns a non-abstinent outcome to those participants for the primary endpoint. It does not tell readers how many participants were lost, whether all outcome assessments were complete, or how missing data were handled for secondary endpoints. Those details are not reported in the registry record.

Secondary outcome group sizes are smaller than the primary outcome group sizes, but the record does not explain why. It would be inappropriate to assume a particular reason, such as attrition, ineligibility, or incomplete assessment. Analysis populations for the secondary endpoints are not reported in the registry record. Without that information, readers cannot fully evaluate selection effects or determine how comparable the analyzed participants were across outcomes.

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: substance abuse (hospital or death) (5.2%), accidents (er or hospital) (3.9%), hospital and respiratory disorder (1.7%), pregnancy complication (1.3%), diabetic complication (1.3%).

The registry reports serious adverse events affecting 3 of 60 participants in the nicotine-replacement group and 10 of 77 in the varenicline group. Other adverse events are reported for 3 of 60 and 1 of 77, respectively. These are group-level counts in the registry record; they do not by themselves establish that the assigned medication caused an event or that the groups differ reliably.

Deaths are not reported in the registry record. The listed serious-event terms include substance abuse (hospital or death), accidents (ER or hospital), hospital and respiratory disorder, pregnancy complication, diabetic complication, and disorientation, with percentages recorded for those terms. The record does not identify which group each listed term belongs to in the summary, so group-specific attribution should not be inferred.

Serious-event counts and other-event counts describe different categories and should be read separately. The available registry information does not provide event timing, participant-level details, exposure-adjusted rates, or a statistical comparison for these safety counts. The figures are descriptive and do not support a causal safety conclusion on their own.

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

The posted primary data show more participants classified as abstinent in the varenicline group than in the nicotine-replacement group at the 3 month follow up. The sponsor reports an odds ratio estimate favoring the varenicline group, but its confidence interval is wide and includes the null value. A recalculation on the risk-difference scale also favors varenicline, but the record flags a discrepancy, so the sponsor’s own analysis takes precedence. The sponsor’s confidence interval and p-value are not readily consistent, and the registry does not explain why.

This result does not establish the size of a stable treatment effect. The confidence interval leaves substantial uncertainty, and the primary endpoint captures a 7-day period rather than sustained abstinence across all follow-up. The result also applies to the recorded comparison in outpatients being treated for substance use disorders, in the setting of the behavioral support described in the registry. It should not be generalized automatically to other populations, treatment settings, regimens, or follow-up periods.

The result does not show whether either regimen produced a particular individual’s outcome, nor does it establish a causal explanation for every observed event. Randomization supports a group comparison, but interpretation still depends on how outcomes were measured and analyzed, how missing data were handled, and whether the posted analysis followed the original plan. Important details on those points are not reported in the registry record.

The secondary outcomes and adverse-event counts add context but do not resolve the primary uncertainty. Secondary analyses are numerous, incompletely reported, and lack a reported multiplicity plan. Safety counts are descriptive and are not accompanied by enough detail for causal attribution. The appropriate reading is therefore limited: the registry shows a difference in observed abstinence counts, alongside uncertainty in the reported effect estimate and incomplete information about broader outcomes and analysis procedures.

18. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the distinction between a point estimate and the precision of that estimate. The primary point estimate favors varenicline, but the sponsor’s confidence interval is wide and includes the null. Readers need to consider the whole interval and the discrepancy between the sponsor’s confidence interval and p-value, rather than relying only on a threshold-based label.

It also illustrates why effect measures matter. An odds ratio and a risk difference answer related but different questions and use different null values. A recalculated result on one scale should not be treated as a direct correction of a sponsor analysis on another scale, especially when the registry flags a discrepancy. Transparent reporting of the estimand, model, and analysis details is important for resolving such differences.

The registry’s missing information is relevant to statistical interpretation. The original sample-size justification, multiplicity approach, planned interim analyses, and analysis populations for secondary outcomes are not reported in the registry record. Such details help readers understand what the study was designed to detect and how secondary findings should be weighed. The planning illustrations based on observed effects do not answer those design questions.

Finally, the trial links a smoking endpoint with a population in substance-use treatment and reports related relapse outcomes. That makes clear why outcome definitions and follow-up windows need careful attention: confirmed 7-day abstinence, continuous abstinence duration, and relapse measures are not interchangeable. The record offers useful observed comparisons, but its limitations in precision and reporting are central to understanding what those comparisons can support.

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.

The primary event counts are limited, and the sponsor’s confidence interval is broad. This leaves uncertainty about the magnitude of the primary contrast. The sponsor’s reported p-value and confidence interval appear inconsistent, and the registry does not explain the discrepancy. Although a simple recalculation is available, it uses a different effect measure and does not supersede the sponsor’s analysis.

The primary endpoint is a point-prevalence measure at the 3 month follow up, based on abstinence during a 7-day window with biochemical confirmation. It does not establish continuous abstinence throughout the study or smoking status after the recorded follow-up. The registry record does not provide a fuller account of follow-up completion, participant flow, or the number lost.

The registry describes an intent-to-treat rule for the primary endpoint, counting people who were lost as smoked. It does not report comparable missing-data rules for secondary outcomes. Secondary analyses include fewer participants than the primary analysis, but reasons for those counts are not reported in the registry record. The analysis populations and missing-data handling for those outcomes are therefore uncertain.

Further limitations include the absence of the original sample-size rationale, full statistical analysis plan, interim-analysis information, and a reported strategy for multiplicity. The secondary results cover only a subset of listed outcomes and have limited precision. Safety information is presented as counts and event terms without sufficient detail about timing or group attribution for each listed term. These reporting limits constrain conclusions about secondary effects and safety.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Varenicline and Motivational Advice for Smokers With Substance Use Disorders — NCT00756275.
• Registry record last updated 2018-08-27; status last verified 2018-07.
• Results first posted 2018-05-08.
• 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.

23. Record Summary

The registry describes a completed randomized, quadruple-masked, parallel-group trial with enrollment of 158 and a primary outcome of 7-day point-prevalence smoking abstinence at the 3 month follow up. The comparison was varenicline with matched placebo patches versus nicotine replacement treatment with a matched placebo pill, in a study that also incorporated behavioral support.

The primary outcome counts were 2 of 60 in the nicotine-replacement group and 10 of 77 in the varenicline group. The sponsor reports an odds ratio of 4.33, with a 95% confidence interval from .91 to 20.56 and p <0.05. The confidence interval includes the null value, and the registry flags a discrepancy with recalculation; the sponsor’s own analysis takes precedence. The record does not explain the apparent inconsistency between its interval and p-value.

Secondary results and serious adverse-event counts are also posted, but they do not resolve the primary uncertainty. Important details about sample-size rationale, multiplicity, missing secondary data, and analysis populations are not reported in the registry record.