Buprenorphine Accumulation and Description of Its Metabolites During Co-Medication of Buprenorphine Transdermal System (BTDS) and Ketoconazole: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Buprenorphine Accumulation and Description of Its Metabolites During Co-Medication of Buprenorphine Transdermal System (BTDS) and Ketoconazole (NCT01259115), a randomized phase 1 study. The primary outcome is AUCt of Buprenorphine With and Without Ketoconazole..

2. Clinical Question

The study asked whether buprenorphine exposure, measured by the area under the plasma concentration-time curve to the last measurable concentration, differed when buprenorphine transdermal system (BTDS) was used with ketoconazole rather than with ketoconazole placebo. Ketoconazole was described in the official study title as a CYP3A4 inhibitor. The primary outcome was AUCt of buprenorphine, reported as a mean in pg/mL*h.

This is a pharmacokinetic question about measured drug exposure in healthy subjects. The record also lists secondary outcomes concerning CYP3A4 inhibition assessed by an erythromycin breath test and the number of participants with adverse events. Those secondary outcomes do not replace the primary AUCt comparison.

3. Trial Design

The registry describes a randomized, double-blind, single-center crossover study in healthy subjects, classified as phase 1. The study is marked completed. Its recorded start was 2002-10 and its primary completion was 2003-06. The registry lists enrollment of 20, while the posted primary-outcome summaries include 18 subjects in the ketoconazole condition and 16 in the placebo condition. These figures refer to different aspects of the record and should not be treated as interchangeable.

A crossover design exposes participants to both treatment conditions in different periods, allowing within-participant comparisons when the relevant measurements are available in both periods. The registry describes two treatment sequences. In Sequence A, subjects received BTDS 10 with ketoconazole 200 mg tablets twice daily in period 1 and BTDS 10 with ketoconazole placebo tablets twice daily in period 2. In Sequence B, the order was reversed. The study was randomized and double-blind; the record does not give further details about how the randomization sequence was generated or how masking was maintained.

The registry describes a washout period of 4 to 18 days between periods. BTDS was worn during days 3 to 10 in period 1 and days 19 to 26 in period 2. Ketoconazole or placebo was taken during days 1 to 11 in period 1 and days 17 to 27 in period 2. The primary outcome timeframe is listed as BTDS days 3, 10, 19, and 26 and ketoconazole or placebo days 9 and 25. These details describe the recorded schedule; the registry does not report a rationale for the particular timing or washout range.

The full analysis population for pharmacokinetics had a defined eligibility rule based on study-drug exposure, emesis, and availability of a valid pharmacokinetic metric. The record does not provide a flow of participants through each period or explain the differences between the overall enrollment and the primary-outcome group sizes. A crossover comparison can be affected by incomplete period data, but which participants contributed paired measurements is 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: Healthy male and female subjects aged 18 to 54 years, demonstrating successful inhibition of CYP3A4 using the EBT (erythromycin breath test) probe were randomized.

Period 1

Reasons for not completing this period:

Period: Washout Period of 4 to 18 Days

Period 2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The full analysis population for pharmacokinetics was defined as those subjects who received at least 1 dose of study drug and did not have any incidents of emesis for at least 12 hours from dosing during at least 1 period and had at least 1 valid pharmacokinetic metric.

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 AUCt of Buprenorphine With and Without Ketoconazole., measured over BTDS Days 3, 10, 19, and 26; ketoconazole or placebo Days 9 and 25.

The primary endpoint was AUCt of buprenorphine, expressed in pg/mL*h. AUCt means the area under the plasma concentration-time curve from hour 0 to the last measurable plasma concentration. It combines concentration measurements across the specified observation interval into a measure of overall observed exposure, rather than describing a concentration at only one sampling time. The registry reports the mean and standard deviation for each treatment condition.

In general, pharmacokinetic endpoints such as AUC are used to compare measured exposure across treatment conditions. AUCt is bounded by the last measurable concentration, so it does not necessarily represent exposure beyond the observation window. The registry does not report the precise concentration-sampling schedule, the handling of values below quantification limits, or the endpoint’s analysis model.

The comparison is between BTDS 10 used with ketoconazole and BTDS 10 used with ketoconazole placebo. Since the patch was used in both conditions, the endpoint addresses the observed buprenorphine exposure under these co-medication conditions, not the effect of BTDS versus no BTDS. The registry also does not report a target difference or a threshold that would define a clinically important change in AUCt. Interpretation therefore rests on the estimated difference and its uncertainty, alongside the limits of the posted summary data.

7. Results Posted in the Registry

• BTDS 10 With Ketoconazole: mean 16,355 versus 16,628 on control; difference -273.10 (95% CI -4,225 to 3,679), standardized effect d = -0.05; z-test p = 0.892.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is continuous, and the registry says it is summarized as a mean with standard deviation. A mean describes the central value of observations in a condition. A standard deviation describes how dispersed individual observations are around that mean. These answer different questions: the means compare average exposure, while the standard deviations describe variability among observations. Neither quantity alone conveys the uncertainty in a between-condition comparison.

What does a mean difference represent?

In general, a mean difference is one condition’s mean minus the other condition’s mean. For this outcome, the posted recalculation uses the ketoconazole condition as the first condition and the placebo condition as the reference. The resulting estimate is -273.1 pg/mL*h. A negative sign therefore indicates that the posted mean in the ketoconazole condition was lower than the placebo-condition mean according to that subtraction order. It does not, by itself, indicate whether the difference is precise, important, or statistically distinguishable from zero.

The calculation is described as unadjusted and based on posted summary statistics. Although the trial used a crossover design, the reported comparison does not document a paired analysis. In general, a paired analysis uses the fact that each participant may contribute measurements under both conditions and can account for within-participant association. A calculation that treats condition summaries without the paired data cannot recover that association. The registry does not report participant-level paired values, a model for period or sequence, or a sponsor’s inferential analysis. The posted mean difference should therefore not be presented as a documented crossover-model estimate.

How should the p-value be read?

In general, a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be under the assumptions of a statistical model. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. The posted p-value is 0.892 and is labeled unadjusted. It is associated with the recalculated comparison, not with a sponsor analysis reported in the registry. The record does not report a multiplicity adjustment or a broader testing plan, so the p-value should not be interpreted as if those details were known.

A p-value also depends on assumptions about the data and analysis. For a crossover study, relevant details can include whether measurements are paired, how period and sequence are handled, and whether observations are complete. Those details are not reported for the posted inferential comparison. Thus, the p-value is best treated as a feature of the displayed summary-based calculation rather than a definitive test of the study’s design-specific treatment contrast.

What information do the confidence limits add?

In general, a confidence interval gives a range of effect estimates that are compatible with the data under a specified procedure. It provides information about both direction and precision that a point estimate does not. The reported interval extends from -4225.0 to 3679.0 pg/mL*h. Because it includes zero and reaches values on both sides, it does not isolate a single direction of difference. Its breadth also matters: estimates quite different from the point estimate remain within the reported limits. The confidence level and the method used to calculate the interval are not reported in the registry record.

Why does variability matter?

In general, greater variation among observations makes it harder to estimate a mean precisely when other design features are held constant. Here, the reported standard deviations are 6197.0 and 5560.0 pg/mL*h, and the outcome group sizes are 18 and 16. In a crossover study, precision can also depend on the correlation between each participant’s measurements across conditions. That correlation is not reported, so the posted standard deviations alone cannot describe the full precision available from a paired analysis.

Over-dispersion is a general concern when observed variation is greater than an assumed statistical model allows. If a model understates variation, it can yield overly narrow intervals or overly optimistic tests. The registry does not report evidence of over-dispersion, a model diagnostic, or an adjustment for it; it is therefore not possible to say that over-dispersion occurred in this study. The general point is that uncertainty estimates rely on assumptions about variation, and the analysis details needed to assess those assumptions are not reported.

What is missing for a full analysis?

The record lists 14 outcome measures and two posted secondary outcomes, but it lists zero posted analyses. It does not report the analysis model for AUCt, the confidence interval level, a prespecified estimand, handling of missing period data, or adjustment for the crossover design. It also does not report how many subjects contributed valid AUCt measurements in both conditions. These omissions limit independent assessment of whether the recalculated comparison matches the intended treatment contrast. The posted summaries remain useful for describing the observed means and the uncertainty calculation, but they do not replace a complete protocol-based analysis.

10. Confidence Intervals and Precision

The reported mean difference was -273.1 pg/mL*h, with an interval from -4225.0 to 3679.0 pg/mL*h. The interval includes zero, so the posted calculation does not resolve whether the average exposure was lower or higher with ketoconazole. Its range also extends well beyond the point estimate in both directions, indicating limited precision for distinguishing modest differences from larger ones. The confidence level for this interval is not reported in the registry record.

In general, a confidence interval reflects uncertainty in an estimate under a particular statistical procedure. It is not a guarantee that the true value lies within the displayed limits, and it does not assign probabilities to individual values after observing the data. Its interpretation depends on the analysis assumptions and method. Those details are especially relevant because the trial is crossover, but the registry does not report a paired analysis or the correlation between measurements from the same subject.

The condition means were 16350.0 pg/mL*h and 16630.0 pg/mL*h, with standard deviations of 6197.0 and 5560.0 pg/mL*h. The group summaries are based on 18 and 16 subjects, respectively. The interval is therefore best read as uncertainty around the recalculated unadjusted difference, not as an interval from a fully documented crossover model. No equivalence margin or clinically important difference is reported. Consequently, the interval cannot establish equivalence, and its inclusion of zero should not be interpreted as proof that the conditions produce identical exposure.

11. 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 planning figures are participants per arm, not total event counts. They are illustrations based on the observed effect, not the trial’s original design assumptions. The listed 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 at the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

In general, power is the probability that a study will detect an effect of a specified size under stated assumptions if that effect is present. The 80% power column gives the planned participants per arm for a calculation targeting an 80% chance of detecting the specified effect under those assumptions. The 90% power column gives the planned participants per arm for targeting a 90% chance. These are planning targets, not guarantees about a future study’s result.

The rows use 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. As the effect used for planning becomes smaller, more participants per arm are needed in the displayed calculations. For example, planning for 75% of the observed effect gives 13,056 participants per arm for 80% power and 17,479 participants per arm for 90% power. These very large illustrations reflect the small observed mean difference relative to the variability and the stated calculation assumptions; they are not prescriptions for a clinical study.

These figures do not show the power achieved by the completed trial. This is not observed power. A sample-size calculation is conditional on its effect and statistical assumptions, and the displayed effect is derived from the observed result rather than a documented original target. The planning display should therefore be read as a sensitivity illustration: smaller target effects call for larger planned groups under the same framework.

12. 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 = -273.100; pooled standard deviation σ = 5907.000.
2. n = 2 × (1.96 + 0.842)² × 5907.000² / -273.100² = 7,343.9, rounded up to 7,344 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 <- -273.100000000002                      # observed difference in means
sigma <- 5907.00041603181                     # 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(1259115)
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 = 7,344 (80% power), 9,832 (90% power)
 75% of observed effect: n per arm = 13,056 (80% power), 17,479 (90% power)
 50% of observed effect: n per arm = 29,376 (80% power), 39,326 (90% power)
power.t.test: 7344.9 
Simulated power at n = 7,344 per arm: 0.799 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists 14 outcome measures and identifies two secondary outcomes: CYP3A4 inhibition assessed by observation of plasma nor-buprenorphine production using the erythromycin breath test, and the number of participants with adverse events. The primary outcome is AUCt of buprenorphine. The record does not provide a complete analysis plan describing how these outcomes were prioritized or tested.

Multiplicity arises in general when multiple outcomes, time points, or comparisons are tested. With more tests, the chance of at least one apparently unusual result can increase if each test is interpreted separately. Statistical approaches can control that risk, but the registry does not report whether any adjustment was planned or performed. The posted p-value is unadjusted. It should not be treated as an adjusted result, and no multiplicity correction should be inferred.

The registry lists zero posted analyses. It does not report the sponsor’s inferential model for the primary outcome, an analysis hierarchy, interim analyses, or prespecified rules for secondary outcomes. Whether interim analyses were conducted is not reported in the registry record. The outcome list alone does not establish how many tests were performed or how their results were used.

The pharmacokinetic analysis population is defined by receipt of at least one study-drug dose, the emesis criterion, and availability of at least one valid pharmacokinetic metric. The primary-outcome summaries report 18 and 16 subjects in the two conditions, but the registry does not provide a period-by-period participant flow or explain why the group counts differ. It does not state how missing measurements were handled, whether measurements were excluded beyond the stated population rule, or how many participants had valid paired observations. These details matter because incomplete data can affect both the composition of the analyzed population and the precision of a crossover comparison.

Consequently, the posted summaries allow a limited description of the primary endpoint but do not establish how missingness, multiple outcomes, or design features were handled in a full analysis. The absence of reported methods is not evidence that no methods were used; it means those methods are not reported in the registry record.

14. 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 4% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event figures report zero affected participants in the BTDS-with-ketoconazole group, among 19 participants at risk, and zero affected participants in the BTDS-with-placebo group, among 17 participants at risk. These are counts of participants with serious adverse events, not counts of all events. No serious adverse event terms are listed in the record.

The registry separately reports other adverse events for 19 participants at risk in the ketoconazole group, with 19 affected, and 17 at risk in the placebo group, with 16 affected. These are not serious adverse event counts and should not be combined with the serious-event figures. The record does not give event types or severity detail in the material reported for these groups. Death counts are not reported in the registry record.

In general, adverse-event counts are descriptive safety information. Zero reported serious events in these groups does not establish that serious events cannot occur, and the group sizes and study setting limit what can be learned from such counts. The adverse-event findings do not answer the primary pharmacokinetic question and should be interpreted separately. The record does not provide enough detail to assess event timing, duration, or attribution to a particular treatment condition.

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

The result describes a small difference between the posted average AUCt values: 16350.0 pg/mL*h with BTDS 10 and ketoconazole and 16630.0 pg/mL*h with BTDS 10 and placebo. The recalculated difference was -273.1 pg/mL*h, and the reported p-value was 0.892. The interval from -4225.0 to 3679.0 pg/mL*h includes zero and spans values in both directions. Taken together, these statistics indicate that the posted summaries do not precisely determine the direction or size of a difference.

This does not demonstrate that the treatments are equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether the uncertainty lies within that margin; neither is reported in the registry record. Nor do these results demonstrate a meaningful increase or decrease in exposure. The interval remains compatible with differences that are larger than the point estimate, and the registry provides no clinical threshold for judging their importance.

The finding is limited to buprenorphine AUCt in healthy subjects under the recorded BTDS and ketoconazole or placebo conditions. It does not directly establish results for other populations, treatment schedules, or clinical outcomes. The record’s secondary outcomes include an erythromycin breath-test measure and adverse events, but the corresponding secondary outcome results are not described in the posted results summarized for this comparison.

The study’s crossover design is relevant because participants were assigned to different treatment sequences and could contribute measurements under both conditions. However, the displayed comparison is a recalculated unadjusted summary, and the record does not report a paired analysis, the correlation between periods, or how incomplete data were handled. Its interval and p-value should therefore be understood as properties of the posted calculation, not as a fully documented analysis of the crossover design.

In general, a non-small p-value does not prove the absence of an effect, and a point estimate near zero does not by itself establish no difference. The most defensible reading is that the observed means were close, while the available summary-based estimate was imprecise. The registry record does not report enough analysis detail to make a stronger conclusion about the treatment contrast.

16. Why This Trial Matters Statistically

This trial illustrates a common statistical distinction in pharmacokinetic research: the observed treatment means can be close while uncertainty about their difference remains substantial. The mean AUCt values were 16350.0 and 16630.0 pg/mL*h, but the recalculated interval extended from -4225.0 to 3679.0 pg/mL*h. Readers therefore need to consider both the estimated difference and its precision, rather than relying on the p-value or the closeness of the means alone.

The crossover design also highlights why analysis details matter. In general, a crossover comparison can use within-participant information, and the association between measurements from the same person may affect precision. The registry describes randomized treatment sequences and a washout period of 4 to 18 days, but it does not report the model used for the primary contrast or whether the posted comparison uses paired observations. A summary-based recalculation cannot reproduce every feature of a design-specific analysis.

The record also separates the overall enrollment from the primary pharmacokinetic group counts. Enrollment was 20, while the condition summaries include 18 and 16 subjects. The stated analysis-population rule explains that valid pharmacokinetic data and other criteria mattered, but a participant flow is not reported. This is a reminder that a trial’s enrollment number does not necessarily describe the population contributing to each endpoint.

Finally, planning illustrations based on a small observed effect can yield very large participant requirements. Such figures help explain how effect size, variability, and target power relate in general, but they are not evidence of the original design rationale and are not observed power. The original sample-size justification is not reported in the registry record. Together, these features make the study useful for teaching careful interpretation of exposure summaries, uncertainty, crossover methods, and planning assumptions.

17. Limitations

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

The primary limitation for interpretation is that the registry reports summary statistics and a recalculated unadjusted comparison, but not a sponsor analysis or the model used to analyze the crossover design. It does not report whether the treatment contrast was estimated using paired measurements, how period or sequence effects were handled, or how within-subject association entered the uncertainty calculation. The reported interval and p-value therefore cannot be verified against a documented design-specific analysis.

The confidence interval level and calculation method are not reported in the registry record. Nor is a clinically important difference or equivalence margin stated. This prevents a formal judgment about equivalence or clinical importance based on the interval. The estimate is also imprecise, with limits that extend in both directions around zero.

There is no participant flow explaining the difference between enrollment of 20 and the primary-outcome condition counts of 18 and 16. Although the pharmacokinetic population criteria are described, the record does not state how many subjects contributed valid paired measurements, why data might be unavailable in a period, or how missing measurements were handled. Those details can affect the interpretation of a crossover comparison.

The study involved healthy subjects and was conducted at a single center, as stated in the official title. The record does not provide evidence to extend these pharmacokinetic summaries to other populations or settings. The available secondary outcome descriptions do not include their numeric results, and serious adverse-event terms are not listed. These omissions mean the primary AUCt summary should not be treated as a complete account of all study outcomes or safety findings.

The original sample-size assumptions and justification are not reported in the registry record. Planning illustrations based on the observed effect cannot fill that gap. In addition, the record lists 14 outcome measures but does not report multiplicity procedures or a complete statistical plan. These limitations concern what can be concluded from the registry record; they do not establish that unreported procedures were absent from the trial conduct.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Buprenorphine Accumulation and Description of Its Metabolites During Co-Medication of Buprenorphine Transdermal System (BTDS) and Ketoconazole — NCT01259115.
• Registry record last updated 2014-05-19; status last verified 2014-05.
• Results first posted 2011-01-26.
• 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.

21. Record Summary

This completed phase 1 study was randomized, double-blind, single-center, and crossover, and enrolled healthy subjects. Its primary question concerned buprenorphine AUCt with BTDS 10 used alongside ketoconazole 200 mg twice daily compared with BTDS 10 used alongside ketoconazole placebo. The registry lists enrollment of 20 and describes two treatment sequences with a washout period of 4 to 18 days.

The posted mean AUCt values were 16350.0 pg/mL*h with ketoconazole and 16630.0 pg/mL*h with placebo. A recalculated unadjusted mean difference was -273.1 pg/mL*h, with a reported p-value of 0.892 and an interval from -4225.0 to 3679.0 pg/mL*h. The registry lists zero posted analyses and does not report a sponsor analysis or the method for a crossover-specific comparison. The result is therefore best read as an imprecise summary-based comparison, not proof of no difference or equivalence.

The record lists an erythromycin breath-test outcome and adverse events as secondary outcomes. Numeric results for those secondary outcomes are not reported in the registry record summarized for this comparison.