EVarQuit: Extended Pre-quit Varenicline to Assist in Quitting Smoking: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for EVarQuit: Extended Pre-quit Varenicline to Assist in Quitting Smoking (NCT03262662), a randomized phase 3 study. The primary outcome is Number of Participants With Continuous Abstinence at End-of-Treatment (EOT) as Assessed by Self-Report and Bio-verification.

2. Clinical Question

3. Trial Design

EVarQuit was a Phase 3 randomized, parallel-group trial with quadruple masking. The registry record lists enrollment of 320 and status as completed. The listed study start was 2017-10-01 and primary completion was 2021-04-05. The sponsor was State University of New York at Buffalo.

The randomized contrast was the timing and duration of varenicline before the target quit date. The Extended Run-In group received 4 weeks of pre-quit varenicline; the Standard Run-In group received 3 weeks of placebo followed by 1 week of pre-quit varenicline. Both groups were planned to receive 11 weeks of varenicline after the target quit date and brief individual cessation counseling. The registry describes the usual varenicline titration in the initial therapy week, then continued dosing thereafter.

The primary outcome was continuous abstinence at end of treatment, assessed through self-report and bio-verification. The registry defines the primary analysis population as intent-to-treat. Secondary outcomes listed include change in cigarettes smoked per day before quitting and continuous abstinence at 6-month follow-up. The record also describes behavioral, physiological, subjective, and real-world electronic momentary assessment measures as part of the study rationale, but does not provide posted analyses for those proposed mechanisms.

The trial description presents extended pre-quit treatment as a hypothesis: a longer period might reduce smoking before the quit date and increase later cessation. That is the rationale being tested, not a finding established by the design description. Details of the original sample-size justification and any planned interim analyses are 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

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat analysis.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Continuous Abstinence at End-of-Treatment (EOT) as Assessed by Self-Report and Bio-verification, measured over Self-report Treatment Weeks 12-15; bio-verification ~Week 16.

The primary endpoint counts participants who met the registry definition of continuous abstinence at end of treatment. Participants had to report no smoking, not even a puff, during the final four weeks of treatment; the registry also required bio-verification, defined as a cotinine level of 15 ng/mL or less. Self-report covered treatment weeks 12-15, with bio-verification at approximately Week 16. The listed analysis population is intent-to-treat.

A continuous-abstinence endpoint captures sustained cessation over a specified period, rather than a single point-in-time report. Requiring both self-report and a biomarker makes the endpoint depend on reported behavior as well as the stated biochemical criterion. The endpoint is clinically interpretable as a count of participants meeting that definition, but the count alone does not describe how abstinence varied over the earlier treatment period or what happened outside the specified assessment window.

The outcome is recorded as a participant count in each randomized group. The registry reports 64 participants meeting the endpoint among 163 in Extended Run-In and 57 among 157 in Standard Run-In. The comparison estimates the difference in the groups’ event proportions and gives a confidence interval to indicate the uncertainty around that estimated contrast. The endpoint does not, by itself, establish the mechanism behind any difference, nor does it represent every possible measure of smoking behavior or longer-term cessation.

7. Results Posted in the Registry

• Extended Run-In: 39.3% (64/163) versus 36.3% (57/157) on control; risk difference 3.0 percentage points (95% CI -7.7 to 13.6), risk ratio 1.08 (0.82–1.43); unadjusted two-proportion z-test p = 0.585.

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.

Pre-quit Change in Cigarettes Smoked Per Day

• 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 errors.
• Result:
  • Extended Run-In: mean -38.80 versus -17.50 on control; difference -21.30 (95% CI -28.92 to -13.68), standardized effect d = -0.69; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Extended Run-In than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With Continuous Abstinence at 6-Month Follow-Up as Assessed by Self-Report and Bio-verification

• 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: 22.7% (37/163) versus 18.5% (29/157) on control; risk difference 4.2 percentage points (95% CI -4.6 to 13.1), risk ratio 1.23 (0.80–1.90); unadjusted two-proportion z-test p = 0.350.
• 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 secondary outcomes address two stages of the study’s rationale: change in smoking before the target quit date and continuous abstinence at follow-up. Together, the posted results show a stronger statistical contrast for pre-quit cigarette reduction than for later abstinence. This pattern is consistent with the distinction between a short-term behavioral measure and a cessation outcome, but it does not establish that change in smoking caused later abstinence or mediated a treatment effect.

The secondary outcomes complement the primary result by showing what happened on other measures and at a different follow-up period. They do not overturn or substitute for the primary end-of-treatment comparison. The primary endpoint remains the central stated outcome, while secondary findings provide additional context about smoking behavior and follow-up. The registry also describes proposed behavioral, physiological, subjective, and electronic momentary assessment measures, but posted analyses for those proposed mechanisms are not reported in the registry record.

Unadjusted secondary results generally carry less weight than a prespecified primary analysis when multiple outcomes are examined. With multiple comparisons, the chance of seeing an apparently notable result by chance can increase. The registry record does not report a multiplicity adjustment or a hierarchy governing interpretation of secondary outcomes. Accordingly, the secondary p-values should be treated as descriptive evidence for their individual outcomes, not as a confirmatory set establishing a broad treatment effect. The record lists no reported analyses for the secondary outcomes, so details about their inferential procedures are not reported in the registry record.

The overall pattern is informative but not conclusive: one secondary measure shows a more pronounced contrast, while the abstinence outcomes retain intervals that include no difference. Differences between measures may reflect their distinct definitions, timing, and scales. The results do not identify the reason for that pattern, and they do not establish that one outcome predicts another at the participant level.

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

• Pre-quit Change in Cigarettes Smoked Per Day
• Number of Participants With Continuous Abstinence at 6-Month Follow-Up as Assessed by Self-Report and Bio-verification

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either met the continuous-abstinence definition or did not. For a binary outcome, a group’s event proportion is the number meeting the definition relative to the group size. The primary comparison reports a risk difference, calculated by subtracting the Standard Run-In proportion from the Extended Run-In proportion. Positive values favor a higher event proportion in Extended Run-In; negative values favor Standard Run-In. The reported estimate is 0.030.

What does the confidence interval express?

A confidence interval communicates statistical uncertainty around an estimated effect. In repeated use of a valid procedure, intervals constructed in the same way would contain the underlying effect at the stated confidence level at the corresponding rate. It is not a guarantee that the particular interval contains the true effect, nor is it a range of individual participant outcomes. The primary interval, -0.077 to 0.136, spans zero, the value corresponding to no risk difference. That breadth means the observed data are compatible with more than one direction and size of effect.

How should the p-value be read?

The unadjusted p-value of 0.585 quantifies how unusual data at least as discordant with a no-difference model would be, if that model and the test assumptions held. It does not give the probability that the null hypothesis is true, and it does not measure the probability that the result will replicate. A p-value should be read alongside the effect estimate and confidence interval. Here, the interval and p-value both indicate that the primary comparison is not precise enough to rule out no difference by the usual null-hypothesis test interpretation.

Why are there additional effect measures?

Risk ratios and odds ratios express binary group contrasts on relative scales, while a risk difference expresses the contrast on an absolute scale. The record lists a risk ratio of 1.081 with interval 0.816 to 1.433 and an odds ratio of 1.134 with interval 0.722 to 1.783 for the primary comparison. These measures answer related but not identical questions. Relative measures can appear larger or smaller depending on the baseline event frequency; absolute and relative scales should not be treated as interchangeable. Their intervals also include the null value for the corresponding scale.

How does the secondary continuous outcome differ?

Pre-quit change in cigarettes smoked per day is reported as a mean and standard error in each group. The posted mean difference is -21.3 percentage points, with a confidence interval from -28.92 to -13.68 and p < 0.001. The negative sign reflects the direction used in the reported contrast, Extended Run-In minus Standard Run-In. The standard error describes uncertainty in an estimated mean, not the spread of individual participant observations. A standard deviation instead describes variation among observations. These quantities answer different questions and should not be substituted for each other.

Why can variability matter?

General statistical explanation: when outcomes vary more than a model assumes, standard errors and tests based on that model can give misleading uncertainty. For count outcomes, over-dispersion means that observed variation exceeds the variation expected under a simple count model; an analysis that accounts for it can produce more realistic uncertainty. The primary endpoint is a participant count meeting a binary definition, and the record does not report an over-dispersion model. That concept should not be mistaken for a feature established in this trial.

What can be concluded from the analysis record?

The primary outcome’s population is identified as intent-to-treat, but the detailed statistical analysis plan is not reported in the registry record. The record lists no reported secondary analyses, despite posted summaries for the secondary outcomes. Specific methods for missing data, covariate adjustment, subgroup analysis, and multiplicity are not reported. The displayed comparisons are therefore best read as the posted unadjusted contrasts rather than as evidence of a more elaborate adjusted analysis. The record does not report whether any interim analysis was planned or conducted.

Planning calculations based on observed effects are a separate exercise from an analysis of trial outcomes. They illustrate how sample size relates to a specified effect and assumptions, rather than establish the design rationale or measure the probability that this completed trial detected an effect. The original trial-design assumptions are not reported in the registry record. General concepts can help interpret the posted statistics, but they cannot fill gaps in the record about which methods were prespecified or used.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.030, and its confidence interval extends from -0.077 to 0.136. The interval includes zero and spans values favoring either group. Its width indicates that the result does not locate the underlying difference precisely. The unadjusted p-value of 0.585 is consistent with the interval’s inclusion of no difference under the reported comparison.

Precision is not the same as whether a result is statistically significant. A narrow interval can still include a small effect, and a point estimate alone can conceal substantial uncertainty. For this primary outcome, the interval allows a range of plausible contrasts wider than the point estimate. The registry results therefore do not support a precise estimate of the size or direction of the between-group difference.

The six-month abstinence comparison is also uncertain: its risk difference is 0.042, with a confidence interval from -0.046 to 0.131. The pre-quit cigarettes-per-day comparison has a confidence interval from -28.92 to -13.68 around a mean difference of -21.3. These intervals concern different endpoints and scales, so their widths should not be compared as if they measured the same quantity.

Confidence intervals reflect sampling uncertainty under the analysis method; they do not account automatically for every possible source of bias, measurement error, missing data, or selective reporting. The registry record does not report enough analysis detail to assess all such assumptions. The intervals are useful measures of statistical precision, but they are not a complete assessment of the certainty or generalizability of the findings.

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 derived from the observed effect, not the original design justification. For the binary outcomes, the listed figures are participants per arm. The registry’s stated calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The record notes that time-to-event tables would report total events, but the outcomes are not time-to-event outcomes. The original trial’s sample-size assumptions are not reported in the registry record.

The 80% power column represents a planning scenario in which a study using the stated assumptions would have an 80% chance of detecting the specified effect with the stated test procedure, if that effect were the true effect and the assumptions held. The 90% power column describes the analogous scenario with a higher chance of detection. These are design probabilities, not guarantees about any particular study or result. They should be read as hypothetical planning targets rather than explanations of the trial’s findings.

Rows for planning for 100%, 75%, and 50% of the observed effect show how the required number changes as the target effect becomes smaller. Smaller effects are harder to distinguish from random variation and therefore require more participants per arm under otherwise fixed assumptions. The displayed curve follows the same general planning relationship; it does not show observed outcomes or a trajectory of participants enrolled. This is not observed power. It is an illustration based on the effect and assumptions specified for the calculation, and it should not be used to infer the probability that the completed trial’s result is true.

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 = 0.363; treatment proportion p₁ = 0.393; average p̄ = 0.378.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6857 = 1.3439.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6854 = 0.5768.
4. n = (1.3439 + 0.5768)² / (0.0296)² = 4,216.1, rounded up to 4,217 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 <- 0.363057324840764                          # control proportion
p1 <- 0.392638036809816                          # 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(3262662)
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 = 4,217 (80% power), 5,644 (90% power)
 75% of observed effect: n per arm = 7,467 (80% power), 9,996 (90% power)
 50% of observed effect: n per arm = 16,735 (80% power), 22,403 (90% power)
power.prop.test: 4216.1 
Simulated power at n = 4,217 per arm: 0.796 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study assesses several outcomes, time points, or comparisons. Even if each test is interpreted separately, considering many tests can increase the chance of at least one result appearing unusual by chance. Prespecified testing hierarchies, adjusted significance thresholds, or other methods can address that issue, depending on the trial’s aims. The registry record does not report a multiplicity strategy, so the unadjusted secondary p-values should not be read as if they necessarily preserve a single overall error rate across all outcomes.

The primary endpoint is identified as an intent-to-treat analysis. That designation indicates the stated analysis population, but it does not by itself explain how participants with missing outcome information were handled. The missing-data method, assumptions about missing outcomes, and any sensitivity analyses are not reported in the registry record. The posted event counts therefore cannot establish whether missing observations were imputed, treated as smoking, excluded, or handled by another procedure.

Missing outcome information can matter for a binary abstinence endpoint because the classification of participants without an observed assessment may affect group event proportions. General statistical explanation: conclusions can depend on whether missingness is related to outcome status or treatment assignment. Sensitivity analyses can examine how conclusions change under different assumptions, but such analyses are not reported in the registry record.

The record also does not report a detailed analysis plan, interim analyses, covariate adjustment, or a prespecified approach to secondary-outcome interpretation. It gives no reported secondary analyses. These omissions limit the ability to determine which analyses were planned in advance and how the posted results relate to any prespecified testing strategy. They do not establish that appropriate procedures were absent; they mean that those procedures are not reported in the registry record.

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: pyelonephritis/nephrolithiasis (0.7%), bilateral hand swelling (0.7%), urinary tract infection (0.7%), scabies (0.7%), urinary frequency and incisional pain 3 days after elective inguinal hernia repair (0.7%).

The registry lists serious and other adverse events separately for each reported study phase and group. For serious adverse events, the listed counts were 0 among 163 at risk in the Extended Run-In group and 0 among 157 at risk in the Standard Run-In group during the pre-treatment phase; 1 among 157 and 0 among 147, respectively, during the pre-quit run-in manipulation phase; and 2 among 150 and 2 among 146 during the early quit phase. The listed death count was 0 in each of these group-phase entries.

These are phase-specific counts, not a single count of all participants who experienced an event across the entire trial. A participant’s exposure and the number at risk differ by phase, so the entries should be read in their stated phase context. The registry also lists other adverse-event counts for each phase, but those are separate from the serious adverse-event counts. Terms listed among serious adverse events include pyelonephritis/nephrolithiasis, bilateral hand swelling, urinary tract infection, scabies, urinary frequency and incisional pain after elective inguinal hernia repair, and bowel obstruction/laparotomy for lysis of adhesions. The listed term percentages are registry entries, not estimates of comparative risk. These summaries do not establish whether events were caused by treatment or support a treatment recommendation.

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

The central statistical finding is an uncertain primary comparison. The observed end-of-treatment abstinence counts were 64 of 163 in Extended Run-In and 57 of 157 in Standard Run-In. The reported risk difference is 0.030, but the confidence interval from -0.077 to 0.136 includes zero, and the unadjusted p-value is 0.585. The data do not provide a precise estimate that separates the group contrast from no difference.

This result does not prove that the two strategies are identical. Failure to distinguish a difference from zero is not the same as evidence of equivalence, especially without a reported equivalence margin or analysis plan. Nor does the point estimate alone establish a benefit. It is one estimate from the observed trial data, with uncertainty expressed by its interval.

The secondary results add context but have different meanings. The pre-quit smoking measure concerns change before the target quit date; follow-up abstinence concerns a later assessment. Neither can be used as a substitute for the primary endpoint, and the posted results do not establish that a pre-quit reduction caused later abstinence. The registry’s description of hypothesized mechanisms is a rationale for investigation, not proof that a mechanism operated.

The record also has reporting limits. It does not report missing-data procedures, a multiplicity strategy, or detailed secondary analysis methods. Those gaps make it harder to assess how robust the posted estimates are to analysis choices. The safety summaries are counts by phase and do not establish causation. Overall, the registry describes a randomized comparison and posts outcome summaries, but those summaries alone do not answer every question about precision, analysis conduct, or broader applicability. No treatment recommendation follows from these statistical results.

17. Why This Trial Matters Statistically

This trial poses a useful statistical question because its randomized contrast changes the timing of treatment before a shared quit date, while both groups are described as receiving post-quit varenicline and brief counseling. That design focuses the comparison on extended versus standard pre-quit run-in rather than comparing varenicline with no treatment across the whole study. The interpretation still depends on the defined outcomes, follow-up, and analysis methods.

The primary endpoint combines a sustained self-reported abstinence period with biochemical verification. That makes the endpoint more specific than a single self-report, but it also means that interpretation depends on both components and their assessment. The registry’s explicit abstinence definition and assessment timing help readers understand what the primary count represents.

Statistically, the contrast between pre-quit cigarette reduction and the abstinence outcomes illustrates why endpoints should not be conflated. A stronger contrast on a behavior measured before quitting does not automatically imply a comparably strong contrast in abstinence. The primary confidence interval is central: it shows the range of uncertainty more directly than the point estimate alone.

The posted planning illustrations also highlight an important distinction between retrospective effect-based calculations and an original design justification. They can illustrate how assumed effect size relates to required sample size, but they do not show the trial’s planned power or observed power. Since the original design assumptions are not reported in the registry record, the planning calculations should not be used to infer the investigators’ initial expectations.

Finally, the record makes clear that statistical interpretation depends not only on numerical estimates but on reporting of analysis populations, missing data, and multiplicity. The intent-to-treat population is identified for the primary endpoint, while several analysis details are not reported. That distinction helps readers separate what the registry documents from what remains uncertain.

18. Limitations

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

The registry record does not report the method used to handle missing primary or secondary outcome data, or sensitivity analyses under alternative assumptions. This matters because the primary endpoint is a participant-level classification that depends on both self-report and bio-verification. The record identifies an intent-to-treat population, but that label alone does not specify the treatment of participants without a complete assessment.

The registry does not report a multiplicity strategy, detailed secondary analysis procedures, or whether interim analyses were planned or conducted. It lists secondary outcomes and posts summary comparisons, but no reported secondary analyses are listed. As a result, the relationship between those summaries and any prespecified inferential plan cannot be assessed from the registry record.

The primary confidence interval is broad and includes zero, so the trial’s posted primary result is not a precise estimate of the group contrast. The enrollment was 320, with the primary outcome counts reported for 163 and 157 participants in the groups, but the record does not provide enough information to characterize reasons for differences in assessment availability or the analysis of missing observations.

The outcome definition focuses on continuous abstinence over the final four treatment weeks, with assessment around Week 16. A result for this window does not by itself describe smoking behavior at every point during treatment or establish long-term abstinence. The six-month follow-up outcome is a separate measure with its own uncertainty.

Finally, adverse events are listed by phase and group; these entries do not establish causation and are not a substitute for a comprehensive comparative safety analysis. The registry summary also does not provide enough detail to assess generalizability beyond the described treatment-seeking smoker population.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: EVarQuit: Extended Pre-quit Varenicline to Assist in Quitting Smoking — NCT03262662.
• Registry record last updated 2025-09-26; status last verified 2025-09.
• Results first posted 2023-07-11.
• 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

EVarQuit is a completed Phase 3 randomized, quadruple-masked, parallel-group trial sponsored by State University of New York at Buffalo, with enrollment of 320. It compared 4 weeks of pre-quit varenicline with 3 weeks of placebo followed by 1 week of varenicline; both groups were described as receiving 11 weeks of post-quit varenicline and brief individual cessation counseling.

The primary endpoint was bio-verified, self-reported continuous abstinence during the final four weeks of treatment. The reported risk difference was 0.030, with a confidence interval from -0.077 to 0.136 and an unadjusted p-value of 0.585. The interval includes no difference and indicates substantial uncertainty around the estimate. Secondary outcomes address pre-quit cigarette change and abstinence at follow-up; their results should be interpreted separately from the primary endpoint and with attention to unreported multiplicity and analysis details.