A Relative Bioavailability Study of Quinine Sulfate Capsules Under Fasting and Fed Conditions: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Relative Bioavailability Study of Quinine Sulfate Capsules Under Fasting and Fed Conditions (NCT00727272), a randomized phase 1 study. The primary outcome is Maximum Plasma Concentration (Cmax).

2. Clinical Question

The study focused on relative bioavailability, using peak plasma concentration as a pharmacokinetic measure. Its stated purposes were to compare the capsule product with the tablet product after single doses under fasting conditions and to evaluate the effect of food on the capsule product. This is a comparison of measured drug concentrations in healthy participants; it does not by itself answer questions about clinical outcomes or use in people with a condition.

The registry describes a randomized, double-blind crossover design. In a crossover study, participants receive more than one treatment condition, so comparisons may use information from the same person under different conditions. The registry record does not report the treatment sequence or period-specific results. It describes three conditions: fasting capsules, fasting tablets, and capsules taken after a standardized high-fat breakfast.

3. Trial Design

The registry identifies this as a randomized, double-blind, phase 1 crossover study in healthy participants. Enrollment was 27, and the study status is completed. The listed start and primary completion dates are 2004-02 and 2004-03. A crossover design exposes participants to multiple conditions, which can allow within-participant comparisons. The registry record does not report the randomization sequence, allocation concealment, washout interval, period duration, or how the analysis accounted for the crossover structure.

The three treatment conditions were a single 324 mg dose of quinine sulfate capsules after an overnight fast of at least 10 hours; a single 300 mg dose of quinine sulphate tablets after the same stated fasting interval; and a single 324 mg capsule dose taken 30 minutes after the initiation of a standardized, high-fat breakfast. Each dose was administered with 240 mL of room-temperature water. The registry also lists Treatment A with its dose adjusted to 300 mg for a comparison.

The total enrollment and the analysis counts are not identical. The primary-outcome description says that data for 26 participants were used for Treatments A and C. It says one participant dropped from the study before period III dosing, identified as Treatment B, and was included in the A-versus-C comparison. The arm summaries list 26 participants for Treatment A, 25 for Treatment B, and 26 for Treatment C. The registry record does not give a full participant flow or explain all differences between enrollment and the outcome-specific counts.

Maximum plasma concentration was measured using serial blood samples drawn from one hour before dosing through 48 hours after dosing, at the scheduled times stated in the registry. The registry record does not report the original sample-size justification, a full statistical analysis plan, or whether interim analyses were planned or conducted.

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.

Period I

Washout Period A

Reasons for not completing this period:

Period II

Washout Period B

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Data for 26 of the 27 subjects were used in the statistical analysis for Treatments A and C. The data for one subject, who dropped from the study prior to period III dosing (Treatment B), was included in the comparison of Treatments A versus C. Treatment A, Dose Adjusted to 300 mg was used to evaluate for dose proportionality.

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 Maximum Plasma Concentration (Cmax), measured over serial pharmacokinetic blood samples drawn within one hour prior to dosing (hour 0) and at 0.5, 1, 2, 2.5, 3, 3.5, 4, 5, 6, 7, 8, 10, 12, 16, 24, 36 and 48 hours after dose administration..

The primary endpoint is maximum plasma concentration, abbreviated Cmax, measured in ng/mL. It represents the highest plasma concentration reached after a dose among the concentrations used to characterize the participant’s profile. The registry describes Cmax as the maximum or peak concentration that the drug reaches in plasma.

Pharmacokinetic studies use peak concentration to describe one aspect of drug exposure. Comparing Cmax under fasting and fed conditions can characterize how the measured peak concentration differs in those study conditions. Comparing the capsule and tablet products under fasting conditions addresses a relative-bioavailability question using this particular endpoint. Cmax is not a direct measure of every aspect of exposure: it does not alone describe the full concentration-time profile or clinical outcomes.

Blood samples were scheduled from one hour before dosing, designated hour 0, through 48 hours after administration. The listed post-dose sampling times include early and later observations, which provide the concentration profile from which a peak can be identified. The registry reports group means and standard deviations for Cmax. It does not report individual concentration profiles, medians, or other primary endpoint summaries. It also does not describe the detailed procedure used to derive Cmax from the serial samples.

For this endpoint, the summaries describe average peak concentrations and their spread in each treatment group. A difference in group means is an estimate of the contrast between conditions, not a statement that every participant experienced that difference. The registry record does not specify a threshold for a clinically important Cmax difference.

7. Results Posted in the Registry

• Treatment A, Dose Adjusted to 300 mg: mean 2,080 versus 2,247 on control; difference -166.40 (95% CI -477.93 to 145.13), standardized effect d = -0.29; z-test p = 0.295.
• Treatment B- Quinine Sulphate 300 mg Tabs, Fasting Conditions: mean 2,278 versus 2,247 on control; difference 31.88 (95% CI -281.75 to 345.51), standardized effect d = 0.06; z-test p = 0.842.
• Treatment C - Quinine Sulfate 324 mg Caps, Fed Conditions: mean 2,540 versus 2,247 on control; difference 293.36 (95% CI -71.61 to 658.33), standardized effect d = 0.44; z-test p = 0.115.

8. Statistical Interpretation

9. Statistical Methods Explained

Maximum plasma concentration is a continuous outcome, and the registry reports its mean and standard deviation for each treatment arm. A mean describes the group’s average value; a standard deviation describes how dispersed individual values are around that average. The standard deviation is not the uncertainty in the estimated mean. The uncertainty in a mean also depends on the number of observations and the analysis design.

What does the mean difference represent?

A mean difference expresses the contrast between two group means in the endpoint’s measurement units, here ng/mL. A positive estimate indicates a higher mean for the comparison condition as encoded in the recalculation, while a negative estimate indicates a lower mean. It is an estimate from the observed summaries, not an individual participant’s change and not a statement about every participant.

The comparisons described as recalculated use posted summary statistics and are simple, unadjusted calculations. They do not incorporate a reported adjustment for the crossover design, period, sequence, or within-participant correlation. Those design features can influence uncertainty because outcomes measured in the same participant may be related. The registry record does not report a model for the primary endpoint, so the recalculated contrasts should be interpreted as descriptive unadjusted comparisons rather than as a reconstruction of a trial-specific model.

How should a confidence interval be read?

A confidence interval describes uncertainty around an estimated contrast under the assumptions of the calculation. A narrower interval indicates greater precision; a wider interval indicates less precision. If an interval includes zero, the summary-based data are compatible with no mean difference as well as with differences on either side of zero. That does not prove that the true difference is zero. The intervals reported for these comparisons include zero, and their widths leave uncertainty about the direction and size of the mean contrast.

A confidence interval is not a range containing a fixed proportion of individual participants’ Cmax values. It concerns the estimated mean difference. Individual values can vary more widely, as reflected in the arm-level standard deviations. The registry does not provide participant-level data or distributions that would allow a fuller description of individual variation.

What does a p-value add?

A p-value measures how compatible the observed summary-based contrast is with a specified null model, under the assumptions used for the calculation. Smaller p-values indicate greater incompatibility with that null model, but the p-value does not give the size or practical importance of a difference. It is not the probability that the null hypothesis is true, and it does not establish equivalence when it is not small. The posted comparison p-values are unadjusted. The registry record does not report the trial’s own significance threshold or a primary analysis plan for these comparisons.

Because there are several treatment contrasts and outcomes in clinical research, repeated testing can raise multiplicity concerns. The registry lists three outcome measures but no secondary posted results, and it reports no analysis submissions. It does not state whether the comparisons were prespecified as separate primary questions or whether any multiplicity procedure was planned. Consequently, the unadjusted p-values should not be treated as adjusted evidence across a family of comparisons.

Why does the crossover design matter?

In general, a crossover design can compare different conditions within the same participant. Such an analysis may account for the pairing between observations, which can improve precision when measurements from one person are correlated. A crossover analysis may also need to consider treatment period and sequence, depending on the design and analysis plan. These are general statistical considerations, not details confirmed for this study. The registry record does not report the sequence allocation, washout, period effects, or the statistical model used.

The simple recalculations use arm-level means and standard deviations, but those summaries do not show the covariance between repeated measurements in the same participant. That information is important for a paired or crossover comparison. Thus, the reported recalculated standard errors and intervals are not a substitute for participant-level crossover analysis. The registry’s lack of submitted analyses means that no sponsor-reported model result is available in the record for comparison.

What is not specified?

The original statistical plan, sample-size justification, handling of missing observations, analysis population definitions, treatment sequence, and interim-analysis plans are not reported in the registry record. The primary endpoint description gives a specific account of the available observations for Treatments A and C and the participant who dropped before Treatment B, but it does not provide a complete missing-data analysis. Without those details, it is not possible to determine whether the posted outcome summaries follow a prespecified analysis or how they handle all aspects of the crossover structure.

10. Confidence Intervals and Precision

Precision is reflected in the width of a confidence interval: a wide interval leaves more uncertainty about the contrast, while a narrow interval constrains the range of plausible values more closely under the calculation’s assumptions. Each reported comparison has a confidence interval that includes zero, so the posted estimates do not pinpoint the direction of the mean difference.

For the dose-adjusted capsule comparison, the estimated difference was -166.4 ng/mL, and its 95% confidence interval extended from -477.9 to 145.1. For the fasting tablet comparison, the estimate was 31.88 ng/mL, with an interval from -281.7 to 345.5. For the fed capsule comparison, the estimate was 293.4 ng/mL, with an interval from -71.61 to 658.3. Each interval includes both zero and values in the direction of the point estimate, as well as values in the opposite direction.

The confidence intervals describe uncertainty in unadjusted recalculations from the posted summaries. They do not account for a reported within-participant crossover model, because the registry record does not report such a model or the information needed to reproduce one. The arm-level standard deviations also show that individual Cmax measurements vary around their group means, but they are not confidence intervals for the treatment differences.

Precision should be distinguished from importance. Even a precise estimate would not determine clinical importance without a meaningful threshold, and no such threshold is reported in the registry record. Conversely, an interval that includes zero does not demonstrate equivalence. The results leave uncertainty about the size and direction of the mean contrasts.

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 for 80% power and participants per arm for 90% power; they are not total event counts. The calculation assumes a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It uses the observed effect as a starting point and considers planning for 100%, 75%, or 50% of that observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives an illustrative number of participants per arm for a design that would have an 80% chance of detecting the selected effect under the stated assumptions, if that effect and the assumptions were correct. The 90% column uses a higher target chance of detecting that effect, so its planning figures are larger. For example, planning for 75% of the observed effect requires 332 participants per arm for 80% power and 444 participants per arm for 90% power for the dose-adjusted capsule comparison. These are planning illustrations, not the size of the study groups.

Smaller effects require more participants to distinguish them from random variation at the same power target. That pattern is visible in the planning values for 100%, 75%, and 50% of the observed effect. The number also depends on the observed effect used as the calculation’s starting point; a small observed contrast can produce especially large planning estimates when a fraction of it is used as the target.

These figures are not observed power and do not describe the probability that the completed study found a true effect. They are prospective-style illustrations calculated from observed contrasts, not evidence that the trial was designed with these sample sizes or assumptions.

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 = -166.400; pooled standard deviation σ = 573.088.
2. n = 2 × (1.96 + 0.842)² × 573.088² / -166.400² = 186.2, rounded up to 187 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 <- -166.4                      # observed difference in means
sigma <- 573.088390084811                     # 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(727272)
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 = 187 (80% power), 250 (90% power)
 75% of observed effect: n per arm = 332 (80% power), 444 (90% power)
 50% of observed effect: n per arm = 745 (80% power), 998 (90% power)
power.t.test: 187.2 
Simulated power at n = 187 per arm: 0.796 (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 three outcome measures and no secondary posted results. It reports no submitted analyses. The record therefore does not provide a full account of which outcome was primary in the original analysis plan beyond identifying maximum plasma concentration as the primary outcome, or how the several treatment comparisons were organized statistically.

Multiplicity arises when several hypotheses are tested. In general, conducting multiple tests can increase the chance of obtaining at least one small p-value by chance. Researchers may address this through prespecified testing hierarchies or adjusted thresholds, but whether any such approach was used in this study is not reported in the registry record. The comparison p-values available for the Cmax summaries are unadjusted, and no multiplicity correction is reported. They should be interpreted as individual comparison statistics rather than as a familywise-adjusted set of results.

The registry describes data for 26 of the 27 enrolled participants as used for Treatments A and C. It also states that one participant dropped before period III dosing, identified as Treatment B, and was included in the A-versus-C comparison. The arm summaries list 26 participants for Treatment A, 25 for Treatment B, and 26 for Treatment C. The record does not provide a full accounting of missing data, the reason for the dropout, or a general rule for including participants in each comparison.

In a crossover study, missing a treatment period can affect which within-participant comparisons are available. As a general matter, the analysis population and missing-data method influence how such incomplete records contribute to estimates. The registry record does not specify an intention-to-treat or per-protocol population, a missing-data imputation method, or a sensitivity analysis. The summary data therefore do not establish how missing observations were handled in the original analysis.

The record also does not report interim analyses or stopping rules. The trial status is completed, but that status alone does not establish whether interim looks occurred. These omissions limit assessment of the analysis plan and the potential effect of missingness or multiple testing on the reported comparisons.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports serious adverse events as zero affected participants in each treatment group. The listed numbers at risk were 26 for fasting 324 mg capsules, 25 for fasting 300 mg tablets, and 27 for fed 324 mg capsules. No serious adverse event terms are listed in the record. The death counts are not reported in the registry record.

These figures describe the serious adverse event entries recorded for the stated groups. They do not establish that no adverse effects of any kind occurred. The registry separately lists other adverse events affecting 11 participants in the fasting capsule group, 7 in the fasting tablet group, and 14 in the fed capsule group, but those counts are not serious adverse event counts.

Safety counts should be read with their group denominators and treatment conditions in mind. The number at risk differs across the registry’s groups, and the record does not report further detail about event timing, recurrence, severity beyond the serious-event classification, or causal attribution. These data describe what is posted in the registry and do not support conclusions beyond the recorded event counts.

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

The posted results describe average peak plasma concentrations across three treatment conditions in a small phase 1 crossover study of healthy participants. The arm means were 2247.0 ng/mL for fasting capsules, 2278.0 ng/mL for fasting tablets, and 2540.0 ng/mL for fed capsules; a dose-adjusted capsule summary was also reported as 2080.0 ng/mL. These summaries provide a picture of the observed Cmax values in the analyzed groups.

The recalculated unadjusted comparisons have confidence intervals that include zero. Their point estimates differ in direction and size, but the intervals remain compatible with a range of possible mean differences. The statistics therefore do not establish that the conditions have identical mean Cmax, nor do they establish a clear difference. The registry record does not report equivalence criteria, so a lack of a decisive difference cannot be interpreted as evidence of equivalence.

The findings concern one pharmacokinetic endpoint after single-dose administration under the specified conditions. They do not establish clinical benefit, harm, or effectiveness. Cmax captures the measured peak concentration and does not summarize every dimension of drug exposure or any clinical outcome. The study population was healthy participants, and the registry record does not establish how the findings apply to other populations or treatment settings.

The comparisons available in the record are unadjusted recalculations from group summaries, not a reported participant-level analysis of the crossover design. Because within-participant correlations and treatment periods are not available, the precision estimates should be interpreted cautiously. The record also does not report the original sample-size justification, full statistical plan, missing-data methods, or multiplicity strategy. Those omissions constrain conclusions about the intended inferential analysis.

The defensible interpretation is descriptive: the registry posts these arm-level Cmax summaries and uncertain unadjusted mean contrasts. It does not provide enough information to establish equivalence or to make broader clinical claims.

16. Why This Trial Matters Statistically

This study illustrates how a pharmacokinetic question can be framed as comparisons of a continuous endpoint across treatment conditions. Cmax is expressed in ng/mL, and the reported group means and standard deviations give distinct information: the means describe average peak concentration, while the standard deviations describe variability among observations. Neither by itself establishes how precisely the treatment contrast is estimated.

The crossover design is statistically important because observations from the same participant may be related. In general, a properly specified crossover analysis can use that pairing, while a simple comparison of arm summaries cannot recover the within-participant covariance. The registry record does not report the model or participant-level data, making it important to distinguish the available unadjusted recalculations from a trial-specific analysis.

The confidence intervals reinforce why a point estimate should not be read in isolation. Each comparison has an interval that includes zero and also allows differences in either direction. The estimates are not precise enough to establish that the treatment conditions have the same mean Cmax or to fix the direction of the difference. P-values alone cannot resolve this uncertainty.

The study also provides an example of the limits of registry summaries. The primary endpoint and treatment conditions are described, but the record does not report the original sample-size rationale, crossover analysis plan, missing-data methods, or multiplicity approach. Those details are central to judging whether the reported comparisons align with the design and the questions the trial intended to answer. The distinction between recorded values and the analysis needed for a reliable design-based inference is a useful statistical lesson.

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.

Several limitations arise from the available record. The enrollment was 27, and the primary-outcome description states that 26 participants contributed data for Treatments A and C. The arm-level summaries have different participant counts, and one participant is described as dropping before period III dosing for Treatment B. A complete participant flow and full explanation of the analysis populations are not reported in the registry record.

The primary endpoint results are presented as arm means and standard deviations. Individual observations, paired within-participant differences, and concentration-time profiles are not reported. These omissions prevent an independent assessment of the distribution of Cmax values or a crossover analysis that accounts for repeated measurements within participants. The recalculated comparisons are unadjusted and should not be treated as a substitute for an unreported crossover model.

The registry record does not report the original sample-size justification, prespecified effect of interest, analysis plan, treatment sequence, washout interval, or period and sequence handling. It also does not report an approach to missing data, sensitivity analyses, or multiplicity adjustment. These gaps limit evaluation of whether the sample size and statistical methods were appropriate for the study’s questions.

The study assessed single-dose conditions in healthy participants. The record does not provide evidence about other populations, repeated dosing, clinical outcomes, or the clinical importance of any Cmax contrast. No equivalence threshold is reported. Finally, serious adverse event counts are posted, but deaths are not reported in the registry record, and event details are limited.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: A Relative Bioavailability Study of Quinine Sulfate Capsules Under Fasting and Fed Conditions — NCT00727272.
• Registry record last updated 2010-01-20; status last verified 2010-01.
• Results first posted 2009-12-30.
• 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

The registry record describes a completed, randomized, double-blind, phase 1 crossover study of quinine sulfate formulations and food conditions in healthy participants. Enrollment was 27, with the study listed as starting in 2004-02 and reaching primary completion in 2004-03.

The primary endpoint was maximum plasma concentration (Cmax), measured in ng/mL. The treatment conditions were a 324 mg capsule after fasting, a 300 mg tablet after fasting, and a 324 mg capsule after a standardized high-fat breakfast. The registry reports arm means and standard deviations and includes unadjusted recalculated comparisons with confidence intervals and p-values.

The posted comparisons are imprecise, and their confidence intervals include zero. The registry record does not report the trial’s original statistical plan, sample-size justification, crossover model, or full missing-data and multiplicity procedures. The results are best read as descriptive pharmacokinetic summaries with uncertainty, not as proof of equivalence or as clinical outcome evidence.