A Pharmacokinetic Evaluation of Two Nicotine Patches in Smokers: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Pharmacokinetic Evaluation of Two Nicotine Patches in Smokers (NCT01702519), a randomized phase 1 study. The primary outcome is Area Under the Curve From Time 0 to the Last Quantifiable Sample, AUC(0-t).

2. Clinical Question

3. Trial Design

This was a completed Phase 1 study of nicotine patches in smokers. The registry lists randomized allocation, single masking, and a crossover model, with enrollment of 40. In a crossover study, participants receive more than one treatment according to an assigned sequence, so comparisons can be made within participants as well as between treatment periods. That is a general description of the design; the registry record does not give the sequences, their allocation, or details of the period structure.

The two treatments were the test nicotine patch, which used an alternate supplier’s polyisobutylene adhesive, and the reference nicotine patch, which used the existing adhesive. The primary endpoint was measured after application of the patch assigned for the relevant sequence. The description says patches were applied to the upper back or arm, blood samples were collected at specified times through 32 hours, and the patch was removed after collection of the 24-hour sample. These details describe the endpoint assessment, not the full crossover protocol.

The record lists an enrollment of 40, while the primary Per Protocol Population results show 38 participants in each arm. Since this is a crossover study, the arm counts should not automatically be interpreted as separate sets of participants. The record does not explain the relation between enrollment, participants completing each period, and the analysis counts beyond defining the Per Protocol Population.

The study is marked completed. The start and primary completion are both listed as 2012-03. The registry record does not report the masking procedure, the sequence-generation method, treatment-period duration, washout arrangements, or a detailed statistical analysis plan. Those omissions limit how fully the design can be reconstructed from the posted 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: A total of 128 participants were screened, of which only 40 were randomized into the study. 71 participants did not meet the study eligibility criteria, 4 were lost to follow up, 6 withdrew consent while the remaining 7 were not randomized due to the other reason.

Period 1

Washout Period

Reasons for not completing this period:

Period 2

Analysis population for the primary outcome, as defined in the registry: Per Protocol Population, which consisted of all randomized participants who took at least one dose of the study treatment, did not have any protocol deviation, and provided enough pharmacokinetic data as determined by the pharmacokineticist.

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 Area Under the Curve From Time 0 to the Last Quantifiable Sample, AUC(0-t), measured over Baseline to 32 hours.

The primary endpoint was AUC(0-t), the area under the plasma concentration-time curve from time 0 to the last quantifiable sample. It was calculated from baseline-adjusted nicotine plasma concentrations, with the endpoint timeframe listed as baseline to 32 hours. In general, AUC summarizes drug exposure over the period covered by the concentration measurements: it reflects both the concentrations observed and how those concentrations change over time.

For a patch comparison, exposure is relevant because the study’s stated objective was to compare the nicotine blood profiles produced by the alternate-adhesive and existing-adhesive patches. AUC offers a summary measure of that profile rather than relying on a single blood sample. The record also describes blood collection at multiple time points and specifies that the patch was removed after the 24-hour sample; the endpoint’s stated timeframe nevertheless extends to 32 hours.

The registry reports the endpoint as a mean with standard deviation and gives values for the test and reference groups. The posted description defines the analysis population as randomized participants who took at least one dose, had no protocol deviation, and had enough pharmacokinetic data, as determined by the pharmacokineticist. AUC is only one aspect of a concentration-time profile. The record also lists secondary pharmacokinetic measures, including AUC from zero to infinity and time to maximum plasma concentration, but those measures do not replace the primary endpoint.

7. Results Posted in the Registry

• Test Patch: mean 494.54 versus 528.43 on control; difference -33.89 (95% CI -89.03 to 21.25), standardized effect d = -0.28; z-test p = 0.228.

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.

Area Under the Concentration Time Curve Between Zero and Infinity, AUC (0-inf)

• 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:
  • Test Patch: mean 505.13 versus 541.15 on control; difference -36.02 (95% CI -93.19 to 21.15), standardized effect d = -0.28; z-test p = 0.217.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test Patch and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists four secondary pharmacokinetic outcomes: AUC from zero to infinity, time to maximum plasma concentration, plasma half-life, and rate of elimination. Results are posted for AUC from zero to infinity, while the record indicates four secondary outcomes in total. The secondary endpoint table and plots should be read as additional descriptions of aspects of the nicotine concentration-time profile, not as independent replacements for the primary AUC(0-t) result.

The posted secondary AUC summary has a direction similar to the primary descriptive comparison: the test-patch mean is lower than the reference-patch mean. The unadjusted mean-difference interval for this secondary outcome includes zero. This broad pattern is compatible with the primary summary but does not independently establish equivalence or a meaningful difference. AUC from zero to infinity and AUC(0-t) are related exposure summaries, so their results are not wholly independent confirmations.

Secondary results commonly carry less inferential weight when many outcomes are examined. In general, testing multiple outcomes increases the opportunity for chance findings, and unadjusted p-values do not control that multiplicity. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes. It also does not post reported-analysis entries for the secondary AUC result. Any unadjusted secondary summaries should therefore be considered exploratory and interpreted alongside, rather than in place of, the primary result.

The record lists Tmax, half-life, and elimination rate, but the available secondary values in this record do not include their endpoint-level estimates. Their overall pattern cannot be assessed from the posted numerical information. The presence of an outcome in the registry list does not establish that its result was posted or that it supported the primary analysis. The secondary outcomes may help characterize a pharmacokinetic profile when results are available, but they cannot fill gaps in the primary model details or missing decision criteria.

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

• Area Under the Concentration Time Curve Between Zero and Infinity, AUC (0-inf)
• Time to Maximum Plasma Concentration (Tmax)
• Plasma Half-life (t1/2)
• Rate of Elimination (Kel)

9. Statistical Interpretation

10. Statistical Methods Explained

The main posted result is a treatment ratio, while the accompanying re-calculation is a mean difference. These are distinct ways to summarize a comparison. A treatment ratio expresses one treatment’s exposure relative to the other on a multiplicative scale; a mean difference expresses the absolute separation between group means on the endpoint’s scale. The ratio is particularly relevant to pharmacokinetic comparisons, where relative exposure is often the focus. The registry reports a treatment ratio of 0.946 and a 90% confidence interval from 0.912 to 0.982. It does not state the equivalence bounds or the detailed model behind that estimate.

The re-calculated mean difference is based on the posted arm means and standard deviations. It is a simple, unadjusted summary, not a reconstruction of the sponsor’s full analysis. Its estimate is -33.89, with a 95% confidence interval from -89.03 to 21.25. The unadjusted p-value is 0.228. A p-value describes how compatible the observed data are with a specified null model, given the assumptions of the test. It does not measure the probability that the null hypothesis is true, and a non-small p-value does not prove that treatments are equivalent.

Confidence intervals communicate both the estimated effect and its uncertainty. The 95% interval for the re-calculated mean difference includes zero, which is consistent with a range of possible mean differences that includes no difference. This interval is not the same as the registry’s 90% interval for the treatment ratio: the scales, analyses, and confidence levels differ. The two intervals should not be treated as interchangeable evidence or as competing versions of a single calculation.

The crossover design matters to analysis. In a crossover trial, measurements from the same participant under different treatments are related. A model that accounts for that pairing can use within-participant information, while a simple comparison of arm summaries does not capture the pairing. Period and sequence may also matter in a crossover analysis. The registry record identifies the design as crossover, but it does not report enough model details to evaluate how the sponsor handled pairing, periods, sequences, or possible carryover. No carryover effect should be presumed either present or absent from this record.

The primary endpoint is continuous: it is reported as a mean and standard deviation. Standard deviation describes variation among measured observations, whereas a confidence interval describes uncertainty around an estimated quantity. They answer different questions. The posted standard deviations are 115.1 for the Test Patch and 129.8 for the Reference Patch. The re-calculation uses a pooled standard deviation of 122.6, as well as the posted sample sizes, to express the mean difference in standardized form. That standardized effect is -0.276. These are features of the unadjusted calculation, not outputs of the sponsor’s reported treatment-ratio model.

In general, a pooled standard deviation combines variability estimates across groups when a calculation assumes a common spread. This can be a useful descriptive device for a simple comparison, but it does not make a model appropriate for a crossover design. The calculation also assumes that the posted group summaries are sufficient for the intended comparison. In a paired design, the within-participant covariance can affect uncertainty, and that quantity is not reported. As a result, the re-calculated confidence interval and p-value should be read as approximate unadjusted summaries of the posted means rather than as a replacement for analysis of the original crossover data.

The registry classifies the sponsor’s reported analysis as non-inferiority or equivalence and reports a 90% confidence interval for the treatment ratio. Equivalence reasoning generally asks whether uncertainty about the treatment contrast falls within prespecified bounds. Non-inferiority reasoning generally asks whether the data exclude an unacceptable loss relative to a comparator. These are general descriptions. The registry record does not report the bounds, the rationale for choosing them, or the exact hypothesis-testing procedure. Consequently, the treatment-ratio estimate and interval can be described, but whether they satisfy a formal criterion cannot be determined from the posted information alone.

Several assumptions affect any statistical summary. The unadjusted calculation is based on the posted means, standard deviations, and sample sizes; it does not use participant-level values. It does not account for the randomized sequence, within-participant correlation, or any adjustment terms. The record also does not specify whether the sponsor transformed the endpoint, how missing pharmacokinetic measurements were handled, or whether an alternative analysis population was considered. These details may be important for a pharmacokinetic crossover analysis, but they are not reported in the registry record.

The distinction between estimation and decision is important. Estimation summarizes the observed contrast and its uncertainty. A decision about equivalence or non-inferiority additionally requires criteria set before examining results and a suitable analysis. General statistical principles cannot fill in the trial’s missing criteria. The posted treatment ratio and interval are the available sponsor analysis; the unadjusted calculation is an additional descriptive aid. Neither should be interpreted as a clinical effect or as advice about patch use.

11. Confidence Intervals and Precision

The sponsor-reported treatment ratio is 0.946, with a 90% confidence interval from 0.912 to 0.982. The interval gives a range of values compatible with the observed data under the sponsor’s analysis and its assumptions. It is narrower in scope than a statement that the true ratio has a particular probability of lying within those bounds; a confidence interval is a procedure for expressing statistical uncertainty, not a guarantee about the unknown value.

The unadjusted mean-difference re-calculation is -33.89, with a 95% confidence interval from -89.03 to 21.25. Its width indicates that the posted summary data do not pin down the mean difference precisely. The interval includes zero, but it also allows a range of negative and positive differences. This is a different estimand and confidence level from the sponsor’s ratio analysis, so the intervals cannot be compared as though they were estimates of the same quantity.

The reported group standard deviations are 115.1 for the Test Patch and 129.8 for the Reference Patch. These describe variation in individual measurements, not the precision of the group comparison. The re-calculation uses 38 participants per arm, but the crossover relationship between measurements is not represented in that simple calculation. Since participant-level paired data and the sponsor model details are not posted, the precision of the design-specific contrast cannot be independently assessed.

Precision should also be distinguished from the decision criterion. A confidence interval can be narrow or broad, but an equivalence conclusion requires comparing it with prespecified bounds. Those bounds are not reported in the registry record. The treatment-ratio interval therefore conveys uncertainty about the estimated ratio, while the record leaves the formal interpretation against the study’s intended criterion unresolved.

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 table is a planning illustration based on the observed effect, not the trial’s original design calculation. Its figures are participants per arm for 80% power and participants per arm for 90% power. They are not total event counts. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect.

The 80% power column gives the planned participants per arm for a design that would have 80% power to detect the specified effect under those assumptions. The 90% power column gives the corresponding planning number for 90% power. Power is a property of a planned analysis under specified assumptions; it is not a measure of how likely the observed result is to be correct.

The table shows planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. Smaller effects need more participants to detect with the same power under the stated assumptions. The sample-size illustrations use the unadjusted observed effect, rather than a crossover model reconstructed from participant-level data. The trial’s own original sample-size justification and design assumptions are not reported in the registry record.

These figures are not observed power. They are hypothetical planning values derived from the posted effect estimate and stated calculation assumptions. They should not be read as a claim about what the completed study was originally designed to detect, or as a substitute for interpreting the confidence intervals and the sponsor’s analysis. The curve and table are best used to show how planning requirements change as the target effect becomes smaller.

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 = -33.890; pooled standard deviation σ = 122.639.
2. n = 2 × (1.96 + 0.842)² × 122.639² / -33.890² = 205.6, rounded up to 206 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 <- -33.8899999999999                      # observed difference in means
sigma <- 122.638558922143                     # 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(1702519)
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 = 206 (80% power), 276 (90% power)
 75% of observed effect: n per arm = 366 (80% power), 490 (90% power)
 50% of observed effect: n per arm = 823 (80% power), 1,101 (90% power)
power.t.test: 206.5 
Simulated power at n = 206 per arm: 0.798 (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’s own analysis reports a treatment ratio of 0.946 with a 90% confidence interval from 0.912 to 0.982. It is categorized as a non-inferiority-or-equivalence analysis. This ratio-based result is the sponsor analysis posted for the trial’s pharmacokinetic comparison. The registry does not provide the prespecified bounds, the full model specification, or a p-value for this analysis.

The separate re-calculation uses the posted means and standard deviations to estimate an unadjusted mean difference of -33.89, with a 95% confidence interval from -89.03 to 21.25 and an unadjusted p-value of 0.228. It does not account for the paired crossover structure or reproduce the sponsor’s treatment-ratio method. The two analyses therefore answer related but not identical statistical questions.

The discrepancy flag is false, but that does not make the re-calculation a substitute for the sponsor’s intended analysis. The registry’s treatment ratio and its interval should be presented as the sponsor-reported result; the mean-difference calculation is supplementary and descriptive. The registry record does not provide enough detail to verify the sponsor’s model or determine whether the reported interval met the study’s intended equivalence criteria. The posted analysis can be described faithfully without inferring an unreported decision rule.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports a primary endpoint and lists several secondary pharmacokinetic outcomes. It does not report whether the analysis plan specified a hierarchy among outcomes, adjusted for multiple comparisons, or treated secondary results as exploratory. This matters because repeated testing can increase the chance of apparently notable results arising by chance. Without a stated multiplicity strategy, secondary p-values and intervals should not be treated as though they were confirmatory evidence under a single controlled testing plan.

The primary analysis population is described as the Per Protocol Population. It included randomized participants who took at least one dose of study treatment, had no protocol deviation, and provided enough pharmacokinetic data as determined by the pharmacokineticist. This definition provides useful context, but the registry record does not report a parallel intention-to-treat analysis, a complete participant flow, or the reasons why participants may have been excluded from the Per Protocol Population.

Although the overall enrollment is 40, the primary results show 38 participants in each arm. In a crossover design, arm counts do not by themselves explain how many participants contributed complete paired data or how missing observations were treated. The adverse-event groups have different at-risk counts from the primary efficacy summaries, and the record does not explain the relationship among those denominators. The handling of missing pharmacokinetic samples, incomplete periods, or protocol deviations is not reported in the registry record.

The registry identifies a crossover design, but does not provide the full statistical model, sequence details, period effects, or carryover assessment. It also does not report the sample-size justification or the specific equivalence bounds. Those absences constrain assessment of the primary analysis, the precision, and the intended decision criteria. They should be treated as reporting limitations rather than filled in through assumptions about customary practice.

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 non-serious adverse event terms

The adverse-event listing reports no serious adverse events in either group: 0 of 38 at risk for the Test Patch and 0 of 39 at risk for the Reference Patch. The registry does not list serious adverse-event terms. These are the posted serious-event counts, not proof that serious events are impossible or that the treatments have identical safety profiles.

For other adverse events, the registry reports 22 of 38 participants at risk in the Test Patch group and 26 of 39 in the Reference Patch group as affected. These figures concern the registry’s other-adverse-event category and should not be confused with serious events. The record does not provide event-level detail in the registry record, nor does it give a statistical comparison or a fuller account of severity, timing, or relatedness.

The safety denominators differ from the primary endpoint counts, and the record does not explain that difference. The study was a pharmacokinetic evaluation with enrollment of 40; its posted safety counts should be read within that record and its reporting scope. They do not support broad conclusions beyond the counts shown.

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

This study asks a focused pharmacokinetic question: how nicotine exposure with a patch using an alternate supplier’s polyisobutylene adhesive compares with exposure from a patch using the existing adhesive. The registry posts a treatment ratio of 0.946 with a 90% confidence interval from 0.912 to 0.982. It also posts group means for the primary AUC(0-t) endpoint and a separate unadjusted mean-difference calculation.

These results describe measured exposure in the analyzed participants. They do not, by themselves, establish that the patches are clinically interchangeable or that any patch should be selected. The registry record does not report the equivalence bounds or the detailed criteria needed to interpret the ratio as a formal equivalence conclusion. Nor does it provide enough information to reconstruct the crossover model from participant-level data.

The unadjusted p-value of 0.228 is not evidence that the treatments are identical. A failure to identify a difference in a conventional comparison is not the same as demonstrating equivalence. An equivalence assessment requires the estimate and its uncertainty to be judged against prespecified margins. Those margins are not reported. The sponsor’s ratio interval is the relevant posted analysis for the stated equivalence-oriented objective, but its decision criterion is absent from the record.

The interpretation is also limited by the analysis population and reporting. Primary results are for the Per Protocol Population, and the registry does not explain the relationship between the enrollment count, the posted arm counts, and complete paired observations. Details on missing data and crossover-specific modeling are not reported. The secondary outcomes add context about the intended pharmacokinetic profile, but their multiplicity strategy and complete results are not available in this record.

Accordingly, the careful conclusion is descriptive: the posted sponsor analysis estimates a treatment ratio and uncertainty interval, and the posted unadjusted summary gives a mean comparison. Determining whether those findings satisfy the study’s formal objective requires information not reported in the registry record. This statistical interpretation is not medical advice and does not establish a treatment recommendation.

18. Why This Trial Matters Statistically

This trial illustrates why an analysis should match the scientific question and study design. The objective concerns relative nicotine exposure from two patches, and the sponsor reports a treatment ratio. A simple mean difference is easier to interpret on the endpoint scale, but it is not the same estimand and does not necessarily address the relative-exposure question in the same way.

The crossover design is also central. Measurements from the same participant under different treatments are related, and the analysis may depend on that pairing and on the structure of treatment periods and sequences. A calculation from group summaries cannot recover those relationships. The example therefore shows why the reported design, analysis population, and model details matter when reading a statistical result.

It also shows the difference between a test for a difference and an equivalence question. A non-small unadjusted p-value does not establish that two treatments are sufficiently similar. Equivalence depends on prespecified margins and an appropriate interval-based assessment. The registry reports a treatment ratio and 90% confidence interval, but not the bounds needed to understand the formal decision.

Finally, the page separates observed results from planning illustrations. Sample-size figures based on the observed effect are not evidence about the trial’s original planning or the probability that its findings are correct. Together, these distinctions are useful for reading registry results without treating a descriptive calculation as a complete account of a clinical trial’s statistical analysis.

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 does not report the equivalence margins, the rationale for those margins, or the detailed statistical plan. Without these, the treatment-ratio estimate and its 90% confidence interval can be described, but the formal equivalence decision cannot be independently assessed from the record.

The record identifies a randomized crossover design but does not describe the treatment sequences, period structure, washout arrangements, or model terms. The unadjusted re-calculation cannot account for within-participant correlation or other crossover-specific features. Participant-level data are not available in this record, so the sponsor analysis cannot be reproduced.

The primary result is reported for a Per Protocol Population, defined by dose receipt, protocol adherence, and sufficient pharmacokinetic data. The record does not give a full participant flow, explain the difference between enrollment and endpoint denominators, or describe missing-data handling. It does not report whether other analysis populations were used.

The listed secondary outcomes are not all accompanied by numerical results in the summarized record. A multiplicity strategy is not reported, and the available secondary AUC summary does not provide a sponsor-reported analysis entry. Safety counts are posted, but further event detail and the reason for differing denominators are not available.

These limitations concern reporting and independent interpretability. They do not establish that the underlying study procedures were absent; they indicate only that the relevant details are not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Pharmacokinetic Evaluation of Two Nicotine Patches in Smokers — NCT01702519.
• Registry record last updated 2015-03-20; status last verified 2015-02.
• Results first posted 2015-02-11.
• 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.

23. Record Summary

The registry describes a completed, randomized, single-masked, crossover Phase 1 study in smokers, with enrollment of 40. It compared a nicotine patch with an alternate supplier’s polyisobutylene adhesive against a reference patch with the existing adhesive.

The primary endpoint was baseline-adjusted AUC(0-t), measured from baseline to 32 hours. The Per Protocol Population results show 38 participants per arm. The sponsor-reported treatment ratio is 0.946, with a 90% confidence interval from 0.912 to 0.982. An unadjusted re-calculation reports a mean difference of -33.89, with a 95% confidence interval from -89.03 to 21.25.

The registry record does not report the equivalence margins, the detailed crossover model, or the original sample-size justification. The posted estimates should therefore be interpreted as statistical summaries, not as a complete account of the sponsor’s decision criteria.