Initial Screening of Gemfibrozil as a Novel Treatment for Tobacco Addiction: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Initial Screening of Gemfibrozil as a Novel Treatment for Tobacco Addiction (NCT01876810), a randomized phase 2 study. The primary outcome is Number of Days With Self-report of No Smoking and Breath Carbon Monoxide of <5 PPM During Quit-attempt Weeks.

2. Clinical Question

3. Trial Design

This phase 2 study, NCT01876810, is titled “Initial Screening of Gemfibrozil as a Novel Treatment for Tobacco Addiction.” Its official title describes testing the PPAR hypothesis of nicotine dependence in humans. The sponsor was the Centre for Addiction and Mental Health. The registry gives a start date of 2014-02, a primary completion date of 2016-02, and a status of Completed.

The design is listed as randomized, double masked, and crossover. Participants received gemfibrozil and placebo in treatment periods, with the registry’s safety record identifying the sequences as Gemfibrozil/Placebo and Placebo/Gemfibrozil. Gemfibrozil was given at 600 mg twice daily for two weeks; the placebo was one lactose pill twice a day for two weeks. Details of treatment-period order beyond the listed sequences, washout, masking procedures, adherence, and the handling of period or carryover effects are not reported in the registry record.

The registry states that the study aimed to examine nicotine reinforcement and cue-elicited craving, and also to screen for the ability of gemfibrozil to aid abstinence during a brief quit attempt. It additionally describes examining whether laboratory measures of tobacco dependence predict smoking abstinence. The primary outcome posted is the number of days with self-report of no smoking and breath carbon monoxide below 5 ppm during quit-attempt weeks. The registry lists one secondary outcome measure concerning the percentage of choice of nicotinized cigarettes after one week of treatment.

Enrollment is listed as 28. The outcome summaries list 27 observations for each treatment condition, but how those analysis counts relate to enrollment, exclusions, missing observations, or the crossover analysis population is not reported in the registry record. The original design assumptions and the trial’s prespecified statistical analysis plan are also not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: 1 participant was excluded after enrollment after disclosure of a mental illness which is an exclusion criteria.

Overall Study

Reasons for not completing this period:

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Number of Days With Self-report of No Smoking and Breath Carbon Monoxide of <5 PPM During Quit-attempt Weeks, measured over 1 week in each phase.

The primary endpoint is the number of days during the quit-attempt weeks on which a participant met both parts of the study’s abstinence definition: self-report of no smoking and breath carbon monoxide below 5 ppm. The registry describes the timeframe as one week in each phase. It says the number of days of no smoking was calculated for each participant and verified by daily self-reports and breath carbon monoxide.

This endpoint combines a participant’s report with an objective biomarker threshold. In general, using more than one source of information can make an outcome definition more explicit than relying on self-report alone. The endpoint is expressed in days, so the posted summary uses means and a mean difference. It captures the duration of qualifying abstinence during the brief quit-attempt periods, rather than a long-term smoking outcome. The registry does not report longer-term follow-up for this endpoint.

The measure is relevant to the stated aim of screening gemfibrozil for its ability to aid abstinence during a brief quit attempt. It is distinct from the laboratory outcome of cigarette choice and from the study’s broader aims concerning nicotine reinforcement and cue-elicited craving. A short-period measure can describe behavior during the defined study window, but it does not by itself establish persistence beyond that window. The registry does not report further details on how missing daily reports or breath measurements were handled, or on the analysis population used for the endpoint.

7. Results Posted in the Registry

• Gemfibrozil: mean 0.20 versus 0.00 on control; difference 0.20 (95% CI 0.00 to 0.40), standardized effect d = 0.54; z-test p = 0.046.

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.

The Percentage of Choice of Nicotinized Cigarettes After 1 Week of Treatment

• 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:
  • Gemfibrozil: mean 0.78 versus 0.77 on control; difference 0.01 (95% CI -0.11 to 0.12), standardized effect d = 0.02; z-test p = 0.934.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Gemfibrozil and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary outcome measure: the percentage of choice of nicotinized cigarettes after one week of treatment. Its treatment summaries are close in the posted means, and the recalculated mean difference is 0.005, with a 95% confidence interval from -0.114 to 0.123 and an unadjusted p-value of 0.934. The sponsor-listed analyses report p = 0.9 for both treatment listings and do not provide confidence limits. The posted secondary results therefore do not add a clear contrast to the primary outcome’s descriptive direction. The numerical findings address a laboratory choice measure, not the same abstinence-days endpoint.

Across the posted outcomes, the primary recalculation has a positive mean difference while the secondary recalculation is near zero, with its interval spanning zero. This is a description of the reported pattern, not evidence that one result explains or confirms the other. The outcomes assess different behaviors and were measured in different settings and timeframes. The registry’s broader aims also included nicotine reinforcement, cue-elicited craving, and prediction of abstinence by laboratory measures, but the single posted secondary measure does not cover all those aims.

Secondary findings generally carry less weight than a prespecified primary result because they may be exploratory and may be interpreted among multiple outcomes or analyses. The registry reports three outcome measures and six analyses, while multiplicity adjustment and the prespecified role of each analysis are not reported in the registry record. Without that information, an unadjusted secondary p-value should not be treated as a confirmatory test. The secondary result can offer context about cigarette choice, but it cannot resolve the discrepancy between the primary recalculation and sponsor analysis or establish the broader hypotheses.

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

• The Percentage of Choice of Nicotinized Cigarettes After 1 Week of Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: it is a count of qualifying abstinence days, summarized as a mean. In general, a mean describes the average outcome within a group, while a mean difference expresses the contrast between two group means in the original measurement units. Here, the unit is days. The posted treatment summaries give a mean of 0.2 for Gemfibrozil and 0.0 for Placebo; the recalculated mean difference is 0.2 days.

What does a confidence interval describe?

In general, a confidence interval gives a range of values compatible with the data and the method used to calculate it. It conveys uncertainty in an estimate, rather than the probability that a particular treatment effect is true. The recalculated interval for the primary mean difference is 0.004 to 0.396. It is an unadjusted recalculation from the posted summary statistics. The sponsor’s reported analyses do not include confidence limits, so the interval does not replace or reconstruct the sponsor’s own analysis.

What does a p-value say?

In general, a p-value describes how unusual data at least as incompatible with a specified null model would be if that model and its assumptions held. It does not measure the size or importance of an effect, and it is not the probability that the null hypothesis is true. The recalculated unadjusted p-value for the primary comparison is 0.046. The sponsor’s analyses list p = 0.1. The registry record flags a discrepancy between the sponsor analysis and the recalculation, so the sponsor’s analysis takes precedence. A threshold-based reading of the recalculated p-value alone would ignore that important distinction.

Why does the crossover design matter?

In general, a crossover design exposes participants to more than one treatment condition, which can allow comparisons that account for within-participant data. The observations from the same person are often related; a method that ignores that relationship may not give the same uncertainty estimate as a crossover analysis. Treatment order, period effects, and carryover can also matter. The registry identifies a crossover model and the two treatment sequences in the safety record, but does not report the sponsor’s detailed model, how within-participant correlation was handled, or how period and carryover effects were assessed. The recalculated estimate is therefore an unadjusted summary-statistic comparison, not a reconstruction of the full crossover analysis.

Why can over-dispersion matter?

In general, over-dispersion occurs when outcome variability is greater than a model assumes. If a statistical method understates variability, its uncertainty estimates may be too narrow and inferential results may be misleading. This is a general consideration for count outcomes, but the registry does not report an over-dispersion assessment or identify a count model for this endpoint. The posted mean and standard error summaries alone do not establish whether over-dispersion was present or how the sponsor handled it.

What do the sponsor analyses report?

The registry lists two-sided t-tests, with one result labeled Mean Difference (Final Values) for Gemfibrozil and another labeled Median Difference (Final Values) for Placebo. Each lists p = 0.1, and neither supplies confidence limits. These reported analyses should be distinguished from the recalculated contrast between the posted treatment summaries. The available record does not explain the difference in parameter labels or provide enough detail to reproduce the sponsor’s analysis. Since the discrepancy flag is true, the sponsor analysis takes precedence.

What can be inferred from a secondary analysis?

In general, secondary outcomes can add context by measuring different aspects of a study question, but they are often less central to the primary inference. When several outcomes or analyses are examined, the chance of at least one apparently notable result can increase unless the analysis plan accounts for multiplicity. The registry lists three outcome measures and six analyses, while one secondary outcome measure is posted. Whether adjustments were planned or applied is not reported in the registry record. Secondary results should consequently be treated as exploratory unless their prespecified role and multiplicity approach are clear.

11. Confidence Intervals and Precision

The recalculated primary mean difference is 0.2 days, with a 95% confidence interval from 0.004 to 0.396. The interval describes uncertainty around the unadjusted recalculation based on posted summary statistics. Its lower limit is close to zero, while its upper limit allows a larger positive difference. The range is therefore important context: the point estimate alone does not convey how uncertain the comparison is.

The registry’s sponsor analyses list p = 0.1 and no confidence limits. The recalculated interval should not be treated as the sponsor’s interval or as a substitute for the sponsor’s analysis. The registry flags a discrepancy, and the sponsor’s own analysis takes precedence. The record does not provide enough detail to determine whether the recalculation reflects the crossover structure or the sponsor’s chosen model.

In general, confidence intervals tend to be wider when estimates are less precise and narrower when the data and analysis provide more precision. Precision is not the same as clinical importance: a narrow interval can still cover effects with little practical relevance, while a wide interval can leave substantial uncertainty. The registry does not report a threshold for a meaningful difference in abstinence days, so the posted estimate cannot be judged against a stated clinical-importance boundary.

For the secondary cigarette-choice outcome, the recalculated mean difference is 0.005, with a 95% confidence interval from -0.114 to 0.123. This interval includes zero and spans values on either side of no difference. The sponsor-listed result is p = 0.9 and has no confidence limits. As with the primary endpoint, the recalculation is unadjusted and does not displace the sponsor’s analysis. Precision should be read alongside the design, reporting gaps, and the exploratory role of the secondary outcome.

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 effect, not the trial’s original design calculation. The original design assumptions are not reported in the registry record. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; the effect to detect is set to the stated fraction of the observed effect. These values are participants per arm, not total event counts.

The 80% power column gives the participants per arm in a hypothetical future study under the listed assumptions to have an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding planning figure for a 90% chance. These are planning probabilities under a model, not guarantees about a future result. This is not observed power.

For the primary outcome, planning for 100% of the observed effect gives 53 participants per arm for 80% power and 71 participants per arm for 90% power. Planning for 75% of the observed effect gives 95 participants per arm for 80% power and 127 participants per arm for 90% power. Planning for 50% of the observed effect gives 212 participants per arm for 80% power and 284 participants per arm for 90% power.

The secondary-outcome illustrations are much larger: planning for 100% of the observed effect gives 30,992 participants per arm for 80% power and 41,489 participants per arm for 90% power; the figures increase for the smaller stated fractions of that effect. In general, smaller effects require more participants to detect with the same power and significance level. These illustrations are particularly sensitive to the observed effect, which can be unstable in a small study. They are not a substitute for a design calculation using a prespecified effect size and analysis model. The trial’s own sample-size justification is not reported in the registry record.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.200; pooled standard deviation σ = 0.367.
2. n = 2 × (1.96 + 0.842)² × 0.367² / 0.200² = 53.0, rounded up to 53 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 <- 0.2                      # observed difference in means
sigma <- 0.367423461417477                     # 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(1876810)
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 = 53 (80% power), 71 (90% power)
 75% of observed effect: n per arm = 95 (80% power), 127 (90% power)
 50% of observed effect: n per arm = 212 (80% power), 284 (90% power)
power.t.test: 54 
Simulated power at n = 53 per arm: 0.793 (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. Analyses Reported by the Sponsor

The registry lists sponsor analyses using two-sided t-tests. The Gemfibrozil listing reports a mean difference in final values of 0.2 and p = 0.1. The Placebo listing reports a median difference in final values of 0.0 and p = 0.1. Neither listing gives confidence limits. The record does not explain why the parameter labels differ or provide sufficient detail to reproduce these analyses.

The unadjusted recalculation from the posted treatment summaries gives a mean difference of 0.2 days, a 95% confidence interval from 0.004 to 0.396, and p = 0.046. This recalculation is not the sponsor’s reported analysis. It uses the posted summary statistics and does not establish that it reproduces a crossover analysis or accounts for within-participant dependence.

The registry marks the results as discrepant. In that situation, the sponsor’s own analysis takes precedence; the recalculated result is best treated as a secondary descriptive check rather than the main inferential conclusion. The record does not provide enough information to resolve why the estimates or p-values differ. In particular, the analysis model, treatment-period handling, and assumptions behind the sponsor’s tests are not reported in the registry record. The distinction between the sponsor’s result and the unadjusted recalculation should remain clear whenever the primary outcome is described.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when statistical tests are conducted across several outcomes, time points, subgroups, or analysis choices. In general, the more tests considered, the greater the chance that at least one result appears notable by chance alone. Researchers may address this through prespecified outcome hierarchies, adjusted significance thresholds, or other approaches. The registry lists three outcome measures and six analyses, but whether a multiplicity plan was prespecified or applied is not reported in the registry record. The unadjusted secondary result should therefore be interpreted cautiously, and the primary result should be understood in the context of the sponsor-analysis discrepancy.

The record does not report the full statistical analysis plan, including the planned models, handling of repeated measurements in the crossover design, treatment of period or carryover effects, or planned covariates. It also does not report the trial’s original sample-size assumptions. These gaps prevent an assessment of whether the posted analyses match prespecified methods or whether the analysis choices were made before or after examining the data.

Missing-data handling and analysis populations are not described in sufficient detail. Enrollment is 28, while each treatment summary lists 27 observations. The record does not explain the difference between those counts, identify the reason for any missing observations, or state how incomplete outcome data were treated. It does not specify whether all randomized participants were included in the sponsor’s primary analysis, or how participants with incomplete crossover periods were handled. No assumptions about missing outcomes should be inferred from the summaries.

These reporting limitations matter because the primary endpoint involves daily self-report and breath carbon monoxide verification, and because crossover comparisons may depend on paired observations and treatment sequence. The registry provides outcome summaries but not enough analysis detail to evaluate those issues fully. Consequently, the posted results can be described, but the robustness of the inference and the influence of analytic decisions cannot be established from the registry record.

16. 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 non-serious adverse event terms

The registry reports serious adverse events for the two treatment sequences. In the Gemfibrozil/Placebo group, 14 were listed as at risk and 0 as affected by a serious adverse event. In the Placebo/Gemfibrozil group, 13 were listed as at risk and 0 as affected. Deaths are listed as 0 in both groups, and no serious-event terms are posted.

For other adverse events, the registry lists 8 affected among 14 at risk in the Gemfibrozil/Placebo group and 6 affected among 13 at risk in the Placebo/Gemfibrozil group. These counts are reported by sequence group. The registry does not provide event descriptions for these other adverse events in the listed summary, nor does it explain whether an affected participant could have experienced more than one event.

These safety counts should be read as the registry’s reported record, not as a complete safety evaluation. The record does not report event timing, severity details for non-serious events, attribution to treatment, or the sponsor’s safety-analysis approach. The absence of listed serious events does not establish that no other risks occurred, and the adverse-event counts do not determine whether a treatment is suitable for an individual.

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

The registry’s primary endpoint describes days of qualifying abstinence during short quit-attempt periods. The treatment summaries show means of 0.2 days for Gemfibrozil and 0.0 days for Placebo. The unadjusted recalculation gives a mean difference of 0.2 days and a 95% confidence interval from 0.004 to 0.396. The sponsor’s listed analyses report p = 0.1, and the registry flags a discrepancy. The sponsor’s own analysis takes precedence, so the recalculated contrast should not be treated as the trial’s definitive inferential result.

The figures do not establish whether gemfibrozil increases abstinence, whether any difference is clinically important, or whether the observed pattern would persist beyond the study’s brief quit-attempt weeks. The registry does not report a threshold for a meaningful difference, long-term abstinence results, or the full analysis details needed to assess the discrepancy. A confidence interval from the recalculation communicates uncertainty under that calculation; it does not correct the missing crossover-analysis information.

The posted secondary result concerns the percentage of choice of nicotinized cigarettes in a laboratory paradigm. It measures a different aspect of tobacco-related behavior and cannot stand in for the primary abstinence endpoint. The study’s stated aims also included nicotine reinforcement, cue-elicited craving, and the predictive validity of laboratory measures, but the registry record does not present posted results for all those aims in the outcome information.

These findings are specific to this phase 2 randomized, double-masked crossover study and its reported measures. The record supports careful description of the posted summaries and of the disagreement between the sponsor analysis and the unadjusted recalculation. It does not support a broad claim about treatment effectiveness, long-term outcomes, or applicability beyond the population and study conditions recorded. Clinical decisions require evidence and assessment beyond these registry summaries.

18. Why This Trial Matters Statistically

This trial illustrates why the estimate, its uncertainty, and the analysis used to produce it should be read together. The primary treatment means and the unadjusted recalculation point in a positive direction, but the sponsor’s listed p-value differs and the registry flags that discrepancy. Treating the recalculated p-value as the sole conclusion would erase an important feature of the record. Giving precedence to the sponsor analysis while also describing the recalculation makes the source and limits of each result explicit.

The crossover design adds a statistical issue that is easy to miss when only treatment-level means and standard errors are available. In general, a crossover comparison can use within-participant information, and an analysis that ignores the relationship between repeated observations may have different uncertainty. The registry does not report enough detail to judge how the sponsor handled that structure. This makes the example useful for distinguishing a simple summary-statistic recalculation from a trial-specific model.

The result also shows how a short-term behavioral endpoint differs from a laboratory measure. Abstinence days and cigarette choice address related but distinct questions. A pattern in one cannot automatically be used to confirm the other, especially when the analysis plan and multiplicity approach are not reported.

Finally, the sample-size illustrations depend on the observed effect and are not evidence of the study’s original planning or of achieved power. Their role is to show how planning requirements change under stated assumptions and smaller target effects. The trial record is therefore a useful setting for learning to separate observed summaries, sponsor inference, recalculated estimates, and hypothetical planning calculations.

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 registry record leaves several trial-specific uncertainties. Although the design is identified as randomized, double masked, and crossover, it does not report the detailed randomization procedure, masking implementation, treatment sequence allocation, washout period, or assessment of period and carryover effects. These details are relevant to interpreting treatment comparisons in a crossover study.

The sponsor’s analysis methods are only partly described. The record lists two-sided t-tests and p-values, but no confidence limits for the sponsor analyses, and the parameter labels differ between treatment listings. The model, paired-data handling, and any adjustments are not reported. The record flags a discrepancy with the unadjusted recalculation, which limits reliance on that recalculation for inference.

The relationship between enrollment of 28 and the 27 observations listed for each treatment condition is not explained. The registry does not describe missing-data handling, analysis populations, adherence, or whether all participants completed both treatment periods. It also does not report the original sample-size justification, prespecified statistical plan, or multiplicity handling.

The primary outcome covers a brief quit-attempt timeframe, with one week in each phase. The registry does not report long-term abstinence outcomes in the posted results. It lists three outcome measures and six analyses, but only one secondary outcome measure is posted; the record therefore does not supply results for every stated study aim. Safety reporting includes adverse-event counts but limited detail about event characteristics, timing, or attribution. These limitations constrain interpretation of the registry record and should not be filled in by assumptions.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Initial Screening of Gemfibrozil as a Novel Treatment for Tobacco Addiction — NCT01876810.
• Registry record last updated 2017-04-20; status last verified 2017-04.
• Results first posted 2017-04-20.
• 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

NCT01876810 is a completed phase 2, randomized, double-masked crossover study sponsored by the Centre for Addiction and Mental Health. Enrollment is listed as 28. Gemfibrozil at 600 mg twice daily for two weeks was compared with a lactose placebo taken twice a day for two weeks.

The primary endpoint was qualifying abstinence days during the quit-attempt weeks, based on self-report and breath carbon monoxide below 5 ppm. The unadjusted recalculation gives a mean difference of 0.2 days, with a 95% confidence interval from 0.004 to 0.396 and p = 0.046. The sponsor’s listed analyses report p = 0.1; because the registry flags a discrepancy, the sponsor analysis takes precedence.

The posted secondary result concerns nicotinized cigarette choice after one week of treatment. The registry does not report the original design assumptions, full analysis plan, missing-data methods, or multiplicity approach. The record supports a cautious account of short-term posted outcomes, not a broad conclusion about treatment effectiveness.