Amlodipine-Benazepril 10mg-20mg Capsules in Healthy Subjects Under Fed Conditions: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Amlodipine-Benazepril 10mg-20mg Capsules in Healthy Subjects Under Fed Conditions (NCT00835367), a randomized phase 1 study. The primary outcome is Cmax - Amlodipine.

2. Clinical Question

The central statistical question is a comparison of drug exposure after the two formulations, not a comparison of clinical outcomes or health benefits. Both products were given in the fed condition, so the registry record describes the comparison in that setting. The crossover structure means that treatment order varied: one sequence received the test formulation first and the reference second, and the other sequence received the reference first and the test second. This design can support within-subject comparisons, although the registry record does not report the model or detailed handling of period and sequence effects.

The posted results focus on Cmax for amlodipine as the primary measure, with additional pharmacokinetic measures for benazeprilat. The record does not report a clinical threshold for a meaningful difference in Cmax, or the acceptance limits used in the sponsor’s equivalence analysis. Consequently, the numerical estimates and their precision can be described, but a full judgment against a prespecified equivalence criterion cannot be reconstructed from the registry record alone.

3. Trial Design

This was a randomized, open-label, Phase 1, two-way crossover study in healthy subjects. The registry record gives the enrollment as 68 and status as completed. The study title specifies administration under fed conditions. The listed start and primary completion are both 2004-03; no more detailed schedule is reported in the registry record.

In a crossover trial, participants receive both treatments in different periods, with treatment order randomized between sequences. In this study, one sequence received amlodipine-benazepril in the first period and Lotrel® in the second; the other sequence received Lotrel® first and amlodipine-benazepril second. This arrangement allows a comparison that can account for each participant’s response to both formulations, provided the analysis uses the crossover structure appropriately. The registry record does not describe the statistical model, any washout interval, or how period and sequence were handled.

Masking was listed as none, so the study was open label. The registry record names Teva Pharmaceuticals USA as sponsor. It lists the two drug interventions and identifies healthy subjects as the condition. It does not report additional eligibility criteria, recruitment details, or the setting in which the study took place.

The primary outcome was Cmax for amlodipine, with blood samples collected over a 168 hour period. The record describes bioequivalence as based on Cmax, or maximum observed concentration. Three secondary pharmacokinetic outcomes for benazeprilat are posted: Cmax, AUC0-inf, and AUC0-t, with blood samples collected over a 36 hour period. The record indicates nine outcome measures and nine analyses overall, but only the primary result and three secondary results are specified in the available outcome details.

The record does not report the original sample-size rationale, prespecified statistical analysis plan, protocol deviations, or whether an interim analysis was conducted. Those omissions limit reconstruction of how the trial was planned and how the final analyses were selected. The planning illustrations associated with the posted comparisons are separate from the trial’s original design and should not be treated as evidence of the sample-size method used for enrollment.

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.

First Intervention

Washout

Reasons for not completing this period:

Second Intervention

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: One subject was excluded from all statistical analysis for Amlodipine based on a pre-dose plasma concentration greater than 5% of the Cmax value.

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 Cmax - Amlodipine, measured over Blood samples collected over 168 hour period.

The primary endpoint was Cmax for amlodipine, measured in pg/mL. Cmax is the maximum observed concentration in the blood after administration. It is used in pharmacokinetic comparisons because it captures peak exposure and can inform comparison of the rate of absorption. The registry record says blood samples were collected over a 168 hour period and describes the bioequivalence assessment as based on this maximum observed concentration.

As a general statistical concept, peak concentration is only one aspect of exposure. It does not, by itself, describe the full concentration-time profile or the total amount of drug exposure. Area-under-the-curve measures provide a different view of exposure over time; the record lists AUC0-inf and AUC0-t among the secondary benazeprilat outcomes. The endpoint selected as primary therefore addresses a defined pharmacokinetic feature, rather than every feature of absorption or any clinical outcome.

The registry record reports group means and standard deviations for the primary endpoint, along with a summary-statistic mean difference and its interval. It also reports a sponsor analysis as a ratio of least squares means with a 90% confidence interval. Ratios are commonly used in bioequivalence assessments because they express relative exposure, while the mean difference expresses an absolute concentration difference. The registry record does not identify the equivalence margins, so the ratio estimate and interval cannot be assessed against those limits from the record alone.

The record notes that one subject was excluded from all statistical analysis for amlodipine on the basis of a pre-dose concentration greater than 5% of the Cmax value. It does not provide further information about the endpoint’s measurement procedures, assay, or the handling of other missing or unusable samples.

7. Results Posted in the Registry

• Lotrel®: mean 5,537 versus 5,621 on control; difference -84.50 (95% CI -483.17 to 314.17), standardized effect d = -0.07; z-test p = 0.678.

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.

Cmax - Benazeprilat

• 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:
  • Lotrel®: mean 235.85 versus 226.79 on control; difference 9.06 (95% CI -14.27 to 32.39), standardized effect d = 0.14; z-test p = 0.447.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lotrel® and the control. The interval gives the range of effects that remain compatible with the data.

AUC0-inf - Benazeprilat

• 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:
  • Lotrel®: mean 1,631 versus 1,646 on control; difference -14.63 (95% CI -179.26 to 150.00), standardized effect d = -0.03; z-test p = 0.862.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lotrel® and the control. The interval gives the range of effects that remain compatible with the data.

AUC0-t - Benazeprilat

• 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:
  • Lotrel®: mean 1,598 versus 1,612 on control; difference -13.91 (95% CI -177.84 to 150.02), standardized effect d = -0.03; z-test p = 0.868.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lotrel® and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary endpoints all concern benazeprilat exposure: Cmax, AUC0-inf, and AUC0-t. Across these measures, the registry-reported ratios are close to the reference scale, and their 90% confidence intervals are relatively concentrated around those estimates. The secondary pattern is broadly consistent with the primary endpoint in the sense that the posted results do not describe a large separation in the reported relative measures. This overall observation is descriptive and does not substitute for a prespecified joint interpretation.

These outcomes add information about benazeprilat rather than providing additional measurements of the primary amlodipine endpoint. Cmax addresses peak concentration, while AUC measures summarize exposure over a specified concentration-time interval. Considering multiple pharmacokinetic measures can help describe different features of exposure, but it also creates more than one statistical comparison. Their results should therefore be interpreted alongside, not as replacements for, the primary endpoint.

The registry record does not report whether secondary analyses were adjusted for multiplicity, whether they were prespecified in a statistical analysis plan, or what hierarchy governed their interpretation. Unadjusted secondary results carry less weight as confirmatory evidence because repeated testing can increase the chance of chance findings. This is a general statistical concern, not a claim that any particular result is spurious. The secondary findings are best viewed as supportive descriptive information, with the missing analysis-plan details kept in mind.

The registry record reports a mean and standard deviation comparison as well as a ratio analysis for each posted secondary measure. Those are distinct summaries with different scales. Detailed endpoint-by-endpoint values are available in the posted results, but repeating them would not change the overall reading: the measures provide a coherent descriptive account of benazeprilat exposure, while the record does not supply enough information to establish how they were used in formal decision-making.

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

• Cmax - Benazeprilat
• AUC0-inf - Benazeprilat
• AUC0-t - Benazeprilat

9. Statistical Interpretation

10. Statistical Methods Explained

What does a crossover design contribute?

In general, a crossover design compares treatments by giving each participant both treatments in different periods. Each participant can serve as their own reference, which can reduce the influence of stable differences between people. Randomizing treatment order helps distribute order effects between sequences. These advantages depend on appropriate conduct and analysis. The registry record reports randomization and the two treatment sequences, but does not report the washout interval, a model specification, or how period and sequence effects were assessed. No assumptions about those details can be reconstructed from the posted summaries.

Because the endpoint groups report means and standard deviations but not the within-participant covariance or paired differences, a summary-statistic comparison cannot reproduce all information from a crossover analysis. In general, the correlation between a participant’s responses to the two treatments affects the precision of a paired comparison. The registry-reported ratio of least squares means is a separate sponsor analysis; its detailed statistical method is not reported in the registry record.

What do the means and standard deviations describe?

The primary endpoint is continuous, and the record reports its mean and standard deviation for each treatment group. A mean describes the group’s average observed concentration. A standard deviation describes the spread of individual observations around that average; it is not the uncertainty interval for the mean or for the treatment comparison. The posted primary standard deviations are 1079 pg/mL for amlodipine-benazepril and 1183 pg/mL for Lotrel®. The endpoint summaries are descriptive and do not, by themselves, account for the paired nature of a crossover design.

The summary-statistic comparison gives an estimated mean difference, an interval, and an unadjusted p-value. The estimate is expressed as Lotrel® minus amlodipine-benazepril. A difference of zero would correspond to equal group means on this scale, but that is not the same as a formal equivalence criterion. The p-value is unadjusted, and the registry record does not state a multiplicity procedure or a full analysis plan.

Why report a ratio of least squares means?

For bioequivalence questions, relative exposure is often expressed as a ratio. The sponsor-reported primary estimate is a ratio of least squares means, with a 90% confidence interval. Least squares means are model-based means adjusted according to the analysis model. Their interpretation depends on the model and the contrasts specified. The registry record does not report those details, so the ratio can be quoted and its uncertainty described, but its calculation cannot be independently reproduced from the record.

In general, a bioequivalence assessment compares the confidence interval for a relative measure with prespecified lower and upper acceptance limits. Those limits represent the range regarded as compatible with equivalence for the study’s purpose. The record identifies the analysis as a legacy non-inferiority or equivalence type, but it does not report the acceptance limits or a formal decision. A ratio estimate near the reference scale is not, on its own, sufficient to establish equivalence; both the interval and the criteria matter.

How should the re-calculation be understood?

The displayed re-calculation is a simple, unadjusted comparison from the posted summary statistics. It gives an absolute mean difference for Lotrel® relative to amlodipine-benazepril, with an interval and unadjusted p-value. It is not the sponsor’s model-based ratio analysis and does not include details that are unavailable in the group summaries. Because the study is a crossover, the re-calculation should be regarded as a descriptive cross-check rather than a replacement for a paired or model-based analysis.

In general, a confidence interval gives a range of values compatible with the data under the analysis method and its assumptions. Its width reflects uncertainty as well as the scale and variability of the endpoint. A p-value describes how incompatible the observed data are with a particular null model; it does not give the probability that treatments are equal, nor does it establish equivalence. These concepts answer different questions and should not be blended into a single conclusion.

What is not reported about the statistical plan?

The registry record does not report the detailed statistical method, the equivalence margins, the original sample-size justification, an interim-analysis plan, or the handling of all missing data. It also does not report an adjustment for multiple endpoints. These omissions matter because they prevent a full audit of which analyses were prespecified, how the crossover structure was modeled, and how the sponsor interpreted the confidence interval against its decision criteria. General statistical principles can explain how such methods work, but they do not fill in the missing study-specific choices.

11. Confidence Intervals and Precision

The primary sponsor estimate is a ratio of least squares means of 101.84, and its reported 90% confidence interval runs from 98.22 to 105.59. The interval expresses uncertainty around the model-based relative estimate. It is not a probability statement about the true value, and it does not alone determine equivalence. That judgment requires comparison with prespecified acceptance limits, which are not reported in the registry record.

The summary-statistic re-calculation for the primary endpoint is an absolute mean difference of -84.5 pg/mL, with an interval from -483.2 to 314.2. This range includes both negative and positive values, so the summary-based estimate is compatible with differences in either direction under that calculation. Its span also illustrates that the point estimate should not be interpreted as exact. The interval is not the sponsor’s reported interval and is not on the same scale as the ratio analysis.

As a general concept, a confidence interval combines the estimated effect with its sampling uncertainty under a specified method. Greater precision is usually reflected in a narrower interval, while a wider interval leaves more plausible values consistent with the data. Interpretation also depends on whether the interval is appropriate to the design and whether the analysis assumptions are credible. For a crossover study, within-participant information can affect precision; the registry record does not provide enough detail to assess that aspect of the sponsor analysis.

The posted data therefore support a description of the estimated peak-concentration comparison, but not an independent determination against formal bioequivalence bounds. The sponsor’s 90% interval is the relevant reported interval for its ratio analysis; the acceptance criteria needed to interpret it are absent. The re-calculated interval provides a separate, unadjusted view on the absolute concentration scale.

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 planning figures are expressed as participants per arm, not as total events. They are illustrations based on the observed effect and are not the original trial’s sample-size calculation. The registry record does not report the assumptions used to choose the trial’s enrollment. The planning illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario sets the effect to detect as a stated fraction of the observed effect.

The column for 80% power describes the number of participants per arm that the planning calculation would require for an 80% chance of detecting the specified effect under its assumptions, if that effect and model were correct. The 90% power column gives the corresponding planning requirement for a higher chance of detection. These are prospective planning concepts; they do not describe the probability that this completed study detected an effect.

The planning rows consider 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The lower-effect scenarios require more participants because smaller differences are harder to distinguish from random variation. This pattern is a general feature of statistical planning: when variability and other assumptions are held constant, detecting a smaller effect with a given power generally calls for a larger sample.

The curve and figures should be read as a sensitivity illustration, not as evidence that the trial had adequate or inadequate power. They are calculated from the observed summary-statistic effect and assumptions listed for the illustration, rather than from the original protocol. This is not observed power. The registry record does not report the trial’s original sample-size rationale or design assumptions, so the planning illustration cannot establish what the investigators intended or whether the study met an original target.

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 = -84.500; pooled standard deviation σ = 1132.534.
2. n = 2 × (1.96 + 0.842)² × 1132.534² / -84.500² = 2,819.9, rounded up to 2,820 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 <- -84.5                      # observed difference in means
sigma <- 1132.53378371243                     # 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(835367)
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 = 2,820 (80% power), 3,775 (90% power)
 75% of observed effect: n per arm = 5,014 (80% power), 6,712 (90% power)
 50% of observed effect: n per arm = 11,280 (80% power), 15,100 (90% power)
power.t.test: 2820.8 
Simulated power at n = 2,820 per arm: 0.792 (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 record reports a sponsor analysis for the primary endpoint as a ratio of least squares means: 101.84, with a 90% confidence interval from 98.22 to 105.59. This is the analysis most directly tied to the stated bioequivalence objective. The record does not report the statistical method, acceptance margins, or a sponsor-reported p-value. It therefore does not allow independent reconstruction of the sponsor’s formal decision from the reported estimate alone.

The summary-statistic re-calculation gives an absolute mean difference of -84.5 pg/mL, with an interval from -483.2 to 314.2 and an unadjusted p-value of 0.678. It is a simple, unadjusted calculation from the posted group summaries and is not the same estimand or scale as the sponsor’s ratio. It also does not reproduce the sponsor’s model-based crossover analysis.

The two analyses can be read as complementary descriptions, not competing versions of one number. The sponsor result is the registry-reported analysis for relative exposure; the re-calculation is a transparent descriptive comparison of the posted means. The registry record indicates no discrepancy between them, but that does not make their methods interchangeable. The missing model details and equivalence margins remain important limitations for interpretation.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary endpoint and several secondary outcomes, but does not report a multiplicity adjustment, a testing hierarchy, or a statistical analysis plan specifying how multiple results were to be interpreted. When several outcomes are tested, the chance of at least one apparently unusual result can increase if each is assessed without adjustment. As a general statistical principle, the primary endpoint typically carries the strongest confirmatory role when it was prespecified; secondary analyses may be supportive or exploratory depending on the study plan. The registry record does not provide enough detail to assign those roles beyond the outcome labels.

Missing-data handling is also incompletely described. For the primary amlodipine analysis, the record says one subject was excluded from all statistical analysis for amlodipine because the pre-dose plasma concentration exceeded 5% of the Cmax value. It does not report whether other observations were missing, how missing samples or incomplete profiles were handled, or whether sensitivity analyses were performed. The endpoint group counts differ across the primary and secondary results, but the registry record does not explain every difference. No additional reasons should be inferred.

The record does not report the full analysis population definition, protocol deviations, or whether all randomized participants were included in any particular analysis. It also does not explain how the crossover analysis addressed period, sequence, or carryover considerations. These are relevant design and analysis questions in a crossover study, but their absence from the registry record is not evidence that they were ignored; it means their handling cannot be assessed from the posted information.

The study’s original sample-size assumptions, interim analyses, and detailed statistical plan are not reported in the registry record. The separate planning illustration is not evidence of the original plan. These gaps limit assessment of prespecification, selective reporting, and the robustness of conclusions across analysis choices.

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

The result describes pharmacokinetic measurements after two formulations administered under fed conditions to healthy subjects. The primary endpoint is peak amlodipine concentration. The posted sponsor analysis reports a ratio of least squares means with a 90% confidence interval, while the summary-statistic re-calculation reports an absolute mean difference with an unadjusted interval and p-value. Together, these estimates describe the observed comparison and its uncertainty on two different scales.

These results do not establish a clinical benefit or harm. The study was not described as an outcomes trial, and the primary measure is a blood concentration rather than a patient-centered clinical endpoint. The registry record does not report follow-up for clinical events, symptom outcomes, or long-term safety outcomes. No medical advice should be inferred from the pharmacokinetic estimates.

The results also do not, by themselves, establish formal bioequivalence. The record identifies a bioequivalence objective and reports a ratio analysis, but does not give the acceptance margins or enough methodological detail to verify the formal criterion. A ratio estimate and confidence interval must be interpreted against prespecified limits; a conventional unadjusted p-value for a mean difference answers a different question. Lack of a statistically persuasive difference is not proof of equivalence.

Generalizability is limited by the enrolled population and conditions described in the registry record: healthy subjects and fed administration. The record does not support extrapolation to other populations or settings. Likewise, the posted pharmacokinetic endpoints concern the formulations and measurements assessed in the study; they do not establish performance for other doses, administration conditions, or outcomes.

A reasonable reading is therefore narrow: the registry record documents a randomized crossover comparison of the formulations and reports estimates for peak amlodipine concentration and benazeprilat exposure. The numerical estimates can be described with their uncertainty, but missing equivalence criteria and analysis details prevent an independent formal conclusion about bioequivalence. They should not be converted into claims about clinical effectiveness.

17. Why This Trial Matters Statistically

This study illustrates why an analysis should be matched to the scientific question. The summary-statistic re-calculation expresses an absolute concentration difference, while the sponsor’s reported ratio of least squares means addresses relative exposure. Both can be informative, but they do not answer exactly the same question. The stated bioequivalence objective makes the ratio analysis especially relevant, while its absent acceptance margins prevent a complete independent assessment.

The crossover structure also matters. In general, comparing treatments within the same participants can use information that is not represented by separate group means and standard deviations. Without the paired data or model details, a simple re-calculation is only a partial statistical view. This distinction helps prevent a descriptive calculation from being mistaken for the study’s complete analysis.

The record further shows why a p-value should not be treated as a universal verdict. The unadjusted p-value accompanies a test of a mean difference, whereas equivalence requires a different decision framework based on prespecified margins and an interval. The registry record does not report those margins. Interpreting the p-value as proof of similarity would therefore exceed what the analysis establishes.

Finally, the study’s planning illustration makes clear that sample-size requirements depend on the effect targeted and the assumptions used. Those illustrative figures do not explain the original enrollment decision. Keeping planning calculations separate from trial design and observed results is essential when assessing precision and power. The record provides useful pharmacokinetic estimates, but its missing design and analysis details also demonstrate the limits of registry-level reporting.

18. Limitations

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

The registry record does not report the equivalence margins, detailed statistical model, or full analysis plan. These omissions limit independent verification of the sponsor’s bioequivalence assessment. The reported ratio and 90% confidence interval can be described, but the decision criterion against which they were assessed is unavailable.

The trial was open label, and the registry record does not describe blinding of laboratory or analysis personnel. It also does not report the washout interval, handling of period and sequence effects, or any assessment of carryover. These details are especially relevant to interpreting a crossover study, but their absence from the registry record does not establish how they were handled in practice.

The primary analysis excluded one subject from all statistical analysis for amlodipine because a pre-dose concentration exceeded 5% of the Cmax value. The record does not explain other differences in endpoint analysis counts, or report missing-data sensitivity analyses. The summary-statistic re-calculation cannot recover within-participant covariance from the posted group summaries, so it is not a full substitute for a crossover model.

The population consisted of healthy subjects, and administration was under fed conditions. The registry record does not establish applicability to other populations or administration settings. It also does not report the original sample-size rationale, interim analyses, or multiplicity adjustment for the secondary outcomes. These limitations constrain interpretation without negating the descriptive information that is posted.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Amlodipine-Benazepril 10mg-20mg Capsules in Healthy Subjects Under Fed Conditions — NCT00835367.
• Registry record last updated 2024-08-21; status last verified 2024-08.
• Results first posted 2009-08-18.
• 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

The registry record describes a completed Phase 1, randomized, open-label, two-way crossover study sponsored by Teva Pharmaceuticals USA. It enrolled healthy subjects and compared amlodipine-benazepril 10 mg-20 mg capsules with Lotrel® 10 mg-20 mg capsules under fed conditions. The two sequences received the products in opposite period orders.

The primary measure was amlodipine Cmax, based on blood samples collected over a 168 hour period. The registry reports group summaries, a summary-statistic mean difference, and a sponsor ratio of least squares means with a 90% confidence interval. It also posts three benazeprilat secondary pharmacokinetic outcomes.

The record does not report the equivalence limits, detailed analysis method, original sample-size rationale, or complete handling of missing data and multiplicity. The posted estimates describe pharmacokinetic comparisons, but those omissions limit independent verification of a formal bioequivalence conclusion.