Bioequivalence Study of Dexlansoprazole Capsules From Two Manufacturing Plants: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Bioequivalence Study of Dexlansoprazole Capsules From Two Manufacturing Plants (NCT03131895), a randomized phase 1 study. The primary outcome is Cmax: Maximum Observed Plasma Concentration for Dexlansoprazole.

2. Clinical Question

3. Trial Design

The registry describes NCT03131895 as a Phase 1, randomized, open-label, single-center, single-dose, two-period, two-part crossover study. It was sponsored by Takeda and is listed as completed. The study dates in the record are 2017-04-25 for start and 2017-07-03 for primary completion. Enrollment is listed as 116, and the condition is healthy volunteers.

The study separated the 30 mg and 60 mg comparisons into two parts. In Part 1, participants received 30 mg capsules from TOB and TPC in one of two sequences. In Part 2, participants received 60 mg capsules from those same plants, also in opposite sequences. The regimen descriptions specify a single oral dose on Day 1 of Period 1 after a 10 hour fast, then a minimum of 5 day washout before the other plant’s formulation. The sequence structure allows each participant to receive both plant versions at the assigned dose, although the registry summary does not give the detailed analysis model for handling this paired design.

Open-label means the record does not describe masking of treatment assignment. A crossover design differs from a parallel-group design because participants receive the compared treatments in separate periods. Such designs can account for stable participant-to-participant differences, but analysis also needs to consider period and sequence effects. The protocol’s detailed procedures for those effects are not reported in the registry record. The reported primary endpoint population is the PK set, defined by receipt of at least 1 dose and at least 1 measurable plasma concentration.

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 participants were enrolled in this 2 part study to receive dexlansoprazole 30 milligram (mg) capsules manufactured by Takeda GmbH Plant (Oranienburg, Germany) (TOB) or 30 mg capsules manufactured by Takeda Pharmaceutical Company Ltd. (Osaka, Japan) (TPC) in Part 1 and dexlansoprazole 60 mg capsules by TOB or 60 mg capsules by TPC in Part 2.

Intervention Period 1 (2 Days)

Washout Period (at Least 5 Days)

Reasons for not completing this period:

Intervention Period 2 (2 Days)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The pharmacokinetic (PK) set included all participants who received at least 1 dose of study drug and had at least 1 measurable plasma concentration.

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.

Population: The safety analysis set included all participants who were randomized and received at least 1 dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Cmax: Maximum Observed Plasma Concentration for Dexlansoprazole, measured over Day 1: pre-dose and at multiple time points (up to 24 hours) post-dose.

The primary endpoint is Cmax, the maximum observed plasma concentration of dexlansoprazole, reported as a mean in nanogram/milliliter (ng/mL), with standard deviation as the measure of spread. The measurement schedule is described as pre-dose and multiple time points up to 24 hours after dosing on Day 1. Cmax describes the highest measured concentration during that sampling period. As a pharmacokinetic measure, it characterizes peak plasma exposure; it does not by itself describe clinical benefit or longer-term outcomes.

Comparing Cmax between formulations is relevant to a bioavailability question because differences in the amount or timing of drug entering the circulation can be reflected in the concentration profile. In crossover work, the sponsor’s reported analysis expresses the comparison as a least-squares mean ratio, with a 90% confidence interval. This ratio-based approach is distinct from a simple difference between arithmetic means. The record does not give the protocol’s rationale for choosing Cmax as the primary endpoint, nor does it report the sampling schedule in enough detail to identify each measurement time.

The registry lists three outcome measures, but the posted primary result is Cmax. It does not provide secondary outcome results in the record. Consequently, the endpoint supports an interpretation of measured peak plasma concentration in the study’s PK set, rather than a broad conclusion about every aspect of bioavailability or clinical effect.

7. Results Posted in the Registry

• Dexlansoprazole 30 mg TPC: mean 519.50 versus 515.70 on control; difference 3.80 (95% CI -103.55 to 111.15), standardized effect d = 0.01; z-test p = 0.945.
• Dexlansoprazole 60 mg TOB: mean 1,027 versus 515.70 on control; difference 511.30 (95% CI 337.99 to 684.61), standardized effect d = 1.09; z-test p = <0.001.
• Dexlansoprazole 60 mg TPC: mean 978.60 versus 515.70 on control; difference 462.90 (95% CI 295.03 to 630.77), standardized effect d = 1.01; z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

What does the reported ratio represent? The sponsor used ANOVA and reported a least-squares mean ratio for each same-dose plant comparison. In general, a least-squares mean is a model-based group estimate that can account for terms specified in the analysis model. A ratio compares the estimated value for one formulation with the estimated value for the other on a multiplicative scale. A ratio of 1 represents equality on that scale. Here, the registry reports ratios of 1.044 for 30 mg and 1.018 for 60 mg. The model’s complete formula, included terms, and handling of crossover sequence and period are not reported in the registry record.

Why use an equivalence analysis? General statistical explanation: an equivalence analysis asks whether the plausible difference between treatments is sufficiently limited to lie within predefined bounds. It is not the same question as whether a conventional test can detect a difference. The confidence interval must be considered relative to the prespecified equivalence margins. Although the registry labels both sponsor analyses EQUIVALENCE and reports 90% confidence intervals, the margins and detailed decision rule are not reported in the registry record. The posted p-values should therefore not be interpreted on their own as proof of equivalence.

What does a confidence interval communicate? General explanation: a confidence interval gives a range of values compatible with the data and the analysis assumptions, and conveys the uncertainty of an estimate. A wider interval indicates less precision than a narrower interval. The sponsor’s intervals are on the ratio scale. The recalculated intervals are on the mean-difference scale and use posted summary statistics. Because these are different estimands and analysis approaches, their intervals are not interchangeable.

How do the recalculations differ from the sponsor analysis? The recalculated mean differences are simple, unadjusted comparisons based on arm-level means and standard deviations. They do not reproduce the sponsor’s ANOVA, least-squares means, or crossover analysis. In particular, the posted arm summaries do not retain each participant’s within-person pairing across periods. Ignoring that pairing can change the estimated uncertainty in a crossover study. The recalculations are therefore descriptive checks, not a replacement for the sponsor’s analysis. The registry marks a discrepancy, so the sponsor’s own analysis takes precedence.

The recalculated comparison for 30 mg TPC versus 30 mg TOB has an estimated difference of 3.8 ng/mL and a 95% confidence interval from -103.5 to 111.1. Its p-value is 0.945. The recalculated contrasts involving 60 mg TOB or 60 mg TPC use 30 mg TOB as the reference group; they therefore compare different doses as well as different arms. They should not be interpreted as the 60 mg plant-to-plant contrast. The sponsor’s reported same-dose comparison is the relevant registry analysis for that question.

Why can variability matter? General explanation: standard deviation describes the spread of participant measurements around a group mean. More variability generally makes a group estimate less precise when other aspects of the design are held constant. The arm-level standard deviations are large relative to the means, and the recalculated standard errors also differ across arms. In a crossover design, however, the precision of a treatment contrast depends importantly on the within-participant relationship between measurements. That relationship cannot be recovered from the arm summaries alone.

What is not described? The registry record does not report the full statistical analysis plan, the model terms, the equivalence margins, missing-data procedures, interim analyses, or the trial’s original sample-size justification. It does not describe whether or how multiplicity was handled across outcomes or analyses. The primary PK set definition is reported, but further analysis-population details are not. These omissions limit independent reproduction and assessment of the sponsor’s analysis.

10. Confidence Intervals and Precision

The precision of the sponsor’s plant comparisons is best judged using the reported ratio estimates and their 90% confidence intervals. For 30 mg, the least-squares mean ratio is 1.044 and its interval runs from 0.945 to 1.152. For 60 mg, the ratio is 1.018 and its interval runs from 0.933 to 1.111. Both estimates are close to 1, but the intervals include values on either side of 1. Their interpretation as evidence of equivalence depends on whether the full interval falls within prespecified equivalence bounds. Those bounds are not reported in the registry record.

General explanation: an interval describes uncertainty under the analysis assumptions; it is not a guarantee that the true value lies within the displayed limits. A narrower interval indicates greater precision. The sponsor’s reported intervals are expressed as ratios, while the simple recalculated intervals are expressed as differences in ng/mL. The scales answer related but distinct questions, so their numerical widths should not be compared directly.

The recalculated 30 mg difference is 3.8 ng/mL, with a 95% confidence interval from -103.5 to 111.1. The substantial range indicates limited precision for that unadjusted mean-difference estimate. The recalculated intervals for the 60 mg arms are contrasts against the 30 mg TOB group, not the intended same-dose plant comparison. Arm-level standard deviations are also sizable, but the crossover-specific precision cannot be recovered from independent arm summaries. The sponsor’s model-based results are the appropriate posted estimates for the intended comparisons.

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 illustrations based on the observed recalculated effect, not on the trial’s original design assumptions. For these non-time-to-event comparisons, the figures are participants per arm, rather than total event counts. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario targets a stated fraction of the observed effect. The trial’s own original sample-size justification and design assumptions are not reported in the registry record.

The 80% power column describes the planned number of participants per arm under the stated assumptions for a design with an 80% chance of detecting the assumed effect if that effect is real. The 90% power column uses a higher chance of detection, so it generally calls for more participants under otherwise matching assumptions. These are design-planning quantities, not observed power; observed power is not what the figures measure.

Each row changes the assumed effect being detected. Planning for 75% of the observed effect or 50% of the observed effect means targeting a smaller difference than the full observed estimate. Smaller effects are harder to distinguish from random variation, so they require more participants under the same assumptions. The resulting figures can vary greatly when the observed effect is very small, as in the 30 mg recalculation. The 60 mg recalculations use contrasts against the 30 mg TOB arm, however, so their planning numbers do not represent a direct plant comparison at 60 mg. Planning figures should be read in light of that contrast and the underlying unadjusted method, not as the trial’s enrollment target or a substitute for the sponsor’s crossover analysis.

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 = 3.800; pooled standard deviation σ = 283.573.
2. n = 2 × (1.96 + 0.842)² × 283.573² / 3.800² = 87,417.7, rounded up to 87,418 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 <- 3.79999999999995                      # observed difference in means
sigma <- 283.572706766848                     # 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(3131895)
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 = 87,418 (80% power), 117,028 (90% power)
 75% of observed effect: n per arm = 155,410 (80% power), 208,049 (90% power)
 50% of observed effect: n per arm = 349,671 (80% power), 468,110 (90% power)
power.t.test: 87418.7 
Simulated power at n = 87,418 per arm: 0.795 (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. Analyses Reported by the Sponsor

The sponsor’s reported results are the ANOVA-based least-squares mean ratios for matching doses from the two plants. The 30 mg comparison has a ratio of 1.044, a 90% confidence interval from 0.945 to 1.152, and p = 0.553. The 60 mg comparison has a ratio of 1.018, a 90% confidence interval from 0.933 to 1.111, and p = 0.892. The registry labels both analyses as equivalence analyses.

The recalculated comparisons are simple unadjusted calculations from posted summary statistics. They do not reproduce the sponsor’s analysis model or its use of the crossover structure. The same-dose 30 mg recalculation gives a mean difference of 3.8 ng/mL, but it is not the same estimand as the sponsor’s least-squares mean ratio. The recalculated 60 mg contrasts are against the 30 mg TOB group and therefore do not provide a like-for-like plant comparison at 60 mg. The registry flags a discrepancy between the posted summaries and recalculation. Accordingly, the sponsor’s own analysis takes precedence for interpreting the intended plant comparisons. The equivalence margins remain unreported in the registry record, which limits independent assessment of the sponsor’s equivalence conclusion.

14. Multiplicity, Missing Data and Analysis Populations

The registry reports two sponsor analyses for the primary Cmax outcome: an ANOVA-based equivalence analysis for 30 mg and one for 60 mg. It also lists three outcome measures and six analyses, but secondary outcome results are not posted in the record. The registry does not explain how the sponsor controlled or considered multiplicity across doses, outcomes, analyses, or any other planned comparisons. A multiplicity adjustment or decision strategy is therefore not reported in the registry record.

Multiplicity matters in general because conducting several statistical tests can increase the chance of at least one apparently notable result arising by chance. The appropriate approach depends on the questions and analysis plan. No approach should be inferred from the presence of multiple reported results, and the record does not state whether the two dose-level equivalence comparisons were treated as separate objectives or as part of a broader testing strategy.

The primary analysis population is defined as the PK set: participants who received at least 1 dose and had at least 1 measurable plasma concentration. The registry record does not report how missing concentration measurements were handled, whether participants were excluded for other analysis reasons, or how incomplete crossover periods were treated. It also does not report an intention-to-treat analysis population or a detailed safety analysis-population definition. Although the crossover regimen descriptions include washout and opposite sequences, the statistical handling of period, sequence, or carryover effects is not reported in the registry record.

The original sample-size justification, assumptions for the sponsor’s design, interim analyses, and complete statistical analysis plan are also not reported in the registry record. These missing details constrain assessment of whether the analyses followed prespecified methods and whether uncertainty from multiple comparisons or missing data was addressed.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events in each of the four treatment groups and zero deaths in each group. The numbers listed at risk for serious adverse events are 51 for 30 mg TOB, 55 for 30 mg TPC, 55 for 60 mg TOB, and 56 for 60 mg TPC. These are group-level registry counts; no serious adverse event terms are listed.

Other adverse events are reported for 8 participants in the 30 mg TOB group, 9 in the 30 mg TPC group, 8 in the 60 mg TOB group, and 11 in the 60 mg TPC group. These are not serious adverse event counts. The registry record does not provide further event descriptions in the registry record, so their nature, severity, timing, and relationship to treatment cannot be assessed from these counts.

Zero reported serious adverse events does not establish that serious harms are impossible or that the formulations have identical safety profiles. This was a single-dose study in healthy volunteers, and the registry counts describe observed events in the recorded study groups. They do not support broad conclusions about safety with repeated use or in patients.

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

The registry addresses a focused pharmacokinetic question: whether Cmax differed between dexlansoprazole capsules manufactured at TOB and TPC, assessed separately for 30 mg and 60 mg. The sponsor’s reported model-based ratios are close to 1 for both doses, and the registry labels both analyses as equivalence. The reported 90% confidence intervals quantify uncertainty around those ratios. Without the prespecified equivalence margins, however, readers cannot independently confirm from the registry record whether the intervals meet the sponsor’s equivalence criterion.

The arm-level means provide context but are not substitutes for the sponsor’s analysis. Nor are the simple recalculations a substitute: they do not preserve the paired crossover information, and the recalculated 60 mg contrasts use a 30 mg reference arm. The registry flags a discrepancy, so the sponsor’s own analysis takes precedence for the intended comparisons.

These findings concern plasma concentration after a single dose in healthy volunteers. They do not establish effects on symptoms, clinical outcomes, or safety during longer-term use. They also do not show that all relevant aspects of bioavailability are identical: the primary endpoint discussed is Cmax, and secondary outcome results are not posted in the registry record. The posted data should therefore be understood as evidence from a specific formulation comparison and study setting, with uncertainty and reporting limitations, rather than as a general treatment conclusion.

More broadly, a nonsignificant p-value is not itself proof of equivalence. Equivalence depends on an explicitly chosen margin and an appropriate confidence-interval assessment. The sponsor’s analyses are designated as equivalence analyses, but the margin is not reported in the registry record. That missing information is essential context for interpreting what the sponsor intended the analysis to establish.

17. Why This Trial Matters Statistically

This study illustrates how a manufacturing comparison can be framed as a pharmacokinetic question rather than a clinical-outcome comparison. Cmax captures peak measured plasma concentration, and the crossover design exposes participants to both plant formulations at the assigned dose. The opposite treatment sequences are intended to make the within-participant comparison possible while limiting the influence of stable differences between participants.

It also demonstrates why the form of the estimate matters. The sponsor reports least-squares mean ratios from ANOVA, while straightforward recalculations from group summaries produce unadjusted mean differences. These estimates have different scales and methods. In a crossover study, participant-level pairing can affect precision, and it is lost in published arm-level means and standard deviations. A recalculation can therefore be useful as a descriptive check without reproducing the intended analysis.

The record also highlights an important distinction between a test for a difference and an equivalence assessment. An estimate close to the null value is not enough on its own; the uncertainty interval must be judged against prespecified equivalence margins. Because the registry does not report those margins, interpretation of the labelled equivalence analyses is constrained. Taken together, the design and reporting details make this a useful example of why statistical interpretation should consider the estimand, analysis model, confidence interval, and registry completeness, rather than relying only on a p-value or a comparison of raw means.

18. Limitations

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

The principal limitation for independent interpretation is incomplete reporting of the sponsor’s statistical methods. The registry does not state the equivalence margins, the full ANOVA model, how the crossover structure was handled, or the protocol’s original sample-size justification. It also does not report missing-data procedures, interim analyses, or a multiplicity plan. These gaps prevent a full audit of the equivalence claim and the analysis assumptions.

The recalculations use posted arm-level means and standard deviations rather than participant-level paired data. They cannot account for the within-participant relationship, and the registry flags a discrepancy. The sponsor’s own analysis takes precedence. Additionally, the recalculated 60 mg contrasts compare those arms with 30 mg TOB, rather than comparing the two plants at the same dose. They should not be used to interpret the 60 mg plant comparison.

The study was open-label, single-center, and conducted in healthy volunteers with a single-dose design. The record does not describe the participant characteristics beyond the healthy-volunteer population, so generalizability to patients or other settings is uncertain. The primary endpoint is a pharmacokinetic measure, and secondary outcome results are not posted in the registry record. Safety counts cover the reported study groups but do not establish safety under repeated dosing or in broader populations.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Bioequivalence Study of Dexlansoprazole Capsules From Two Manufacturing Plants — NCT03131895.
• Registry record last updated 2019-06-14; status last verified 2019-03.
• Results first posted 2019-06-14.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT03131895 is a completed Phase 1 randomized, open-label, single-center crossover study sponsored by Takeda. It enrolled 116 healthy volunteers and compared single doses of dexlansoprazole delayed-release capsules manufactured at TOB and TPC, separately at 30 mg and 60 mg. The primary endpoint was mean Cmax, with standard deviation, measured through sampling up to 24 hours after dosing.

The sponsor reported ANOVA-based equivalence analyses for both doses, with least-squares mean ratios and 90% confidence intervals. The registry does not report the equivalence margins or full statistical plan. Unadjusted recalculations do not reproduce the sponsor’s crossover analysis; given the flagged discrepancy, the sponsor’s own analysis takes precedence. The record reports zero serious adverse events and zero deaths in all groups, while other adverse events were also recorded. Findings are limited to the stated pharmacokinetic setting and posted outcomes.