Bioequivalence Study of Two Oral Haloperidol Tablets Formulations in Healthy Subjects Under Fasting Conditions: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Bioequivalence Study of Two Oral Haloperidol Tablets Formulations in Healthy Subjects Under Fasting Conditions (NCT04411940), a randomized phase 1 study. The primary outcome is Concentration Maximum (Cmax).

2. Clinical Question

The clinical question is therefore about similarity in a measured drug-concentration outcome after the two formulations, in healthy participants under the study conditions. It is not a comparison of symptom improvement or other clinical benefit: the population, intervention, and primary outcome describe a pharmacokinetic bioequivalence study. The registry also lists time to maximum concentration, the terminal elimination rate constant, and apparent terminal elimination half-life as secondary outcomes.

A crossover design can compare treatments within participants, which can be useful when the measured outcome varies substantially between people. However, the record does not report the treatment sequence, washout details, or the analysis method used to account for repeated measurements within a participant. Those details matter for assessing how the formal comparison was carried out. The available summary statistics alone do not establish whether the study met a prespecified bioequivalence standard.

3. Trial Design

The registry identifies this as a randomized, single-center, open-label, single-dose, two-period crossover study. It was conducted in healthy males and females under fasting conditions and was classified as phase 1. The stated purpose was to determine whether the Cycle Pharmaceuticals Ltd. test tablets and the Mylan Pharmaceuticals Inc. reference tablets, each containing haloperidol 2 mg, were bioequivalent. The registry lists the study as completed.

In a crossover study, participants receive treatments in different periods rather than being assigned to remain in only one treatment group throughout. Randomization is intended to assign treatment order. The study title confirms a randomized two-period crossover, but the treatment sequences and their allocation are not reported in the registry record. Neither is a washout interval described in the information recorded. Those details are important for evaluating possible carryover and the precise structure of the comparison, and should not be inferred from the word “crossover” alone.

The registry lists 32 enrolled participants and reports 32 in each treatment group for the posted outcome summaries. Because this is a crossover design, those group entries should not be added together or treated as evidence for separate sets of participants. The record does not report the number of participants included in each formal analysis, exclusions, or missing observations.

Both treatment descriptions include benztropine mesylate as pre-medication, with the same dose and schedule. The primary measurement was Cmax, the maximum observed plasma concentration of haloperidol, collected over the stated post-dose sampling schedule. The secondary measures concern the timing of that maximum and elimination from the body. The record lists six outcome measures overall, while the posted outcome descriptions identify the primary measure and three secondary measures.

Although the registry identifies a bioequivalence objective, it does not report the protocol’s original sample-size assumptions, the prespecified acceptance criteria, or the sponsor’s formal statistical analysis. The registry record also does not report an analysis population definition. These omissions limit reconstruction of the planned analysis from the available record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: 32 subjects were enrolled in the study. 29 were excluded from the study. 3 subjects were kept as standbys.

Treatment Period 1 (8 Days)

Washout Period (14 Days)

Treatment Period 2 (8 Days)

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 Concentration Maximum (Cmax), measured over pre-dose (0 hours), and at 0.5, 1, 1.5, 2, 2.5, 3, 3.5, 4, 4.5, 5, 5.5, 6, 8, 12, 16, 24, 30, 36, 48, 72, 96, 120, 144, 168, 192 hours post dose.

Cmax is the maximum observed concentration of haloperidol measured by bioanalysis of blood plasma. It describes the highest concentration observed during the sampling period after a dose. The registry’s primary outcome is reported as a mean with standard deviation, and its timeframe covers pre-dose measurement and multiple post-dose collection times through 192 hours.

Cmax is used in pharmacokinetic comparisons because it captures peak exposure, which can differ between formulations even when the active ingredient and dose are the same. In a bioequivalence study, comparing peak exposure is one part of assessing whether formulations produce sufficiently similar concentration profiles. It is not, by itself, a complete description of exposure over time. A concentration maximum does not show the total exposure represented by an area-under-the-curve measure, and the registry record does not report an area-under-the-curve endpoint in the outcome descriptions.

The posted summaries give a mean and standard deviation for each treatment. These are descriptive statistics: the mean locates the group’s average, while the standard deviation describes variability among observations. Bioequivalence is not established merely because two observed means appear similar or because a conventional test does not detect a difference. A formal conclusion depends on the prespecified analysis and acceptance criteria. Neither is reported in the registry record, so the posted Cmax summary cannot be interpreted as a complete formal bioequivalence decision.

7. Results Posted in the Registry

• Test Product (Treatment B): mean 0.87 versus 0.91 on control; difference -0.04 (95% CI -0.26 to 0.18), standardized effect d = -0.09; z-test p = 0.734.

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.

Time to Maximum Concentration (Tmax)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Test Product (Treatment B): mean 4.41 versus 4.39 on control; difference 0.01 (95% CI -0.49 to 0.52), standardized effect d = 0.01; z-test p = 0.963.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test Product (Treatment B) and the control. The interval gives the range of effects that remain compatible with the data.

Terminal Elimination Rate Constant (λz)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Test Product (Treatment B): mean 0.01 versus 0.01 on control; difference -0.00 (95% CI -0.00 to 0.00), standardized effect d = -0.24; z-test p = 0.331.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test Product (Treatment B) and the control. The interval gives the range of effects that remain compatible with the data.

Apparent Terminal Elimination Half-Life (t½)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Test Product (Treatment B): mean 65.99 versus 62.31 on control; difference 3.68 (95% CI -5.63 to 12.99), standardized effect d = 0.19; z-test p = 0.438.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test Product (Treatment B) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes provide supporting descriptions of the timing and elimination portions of the haloperidol concentration profile. Across time to maximum concentration, terminal elimination rate constant, and apparent terminal elimination half-life, the unadjusted comparisons do not show a clear separation between the treatment summaries: each reported confidence interval includes zero. This broad pattern is compatible with the primary Cmax comparison’s lack of a clear unadjusted difference, but it does not independently establish bioequivalence.

These measures are related to the primary pharmacokinetic question in different ways. Time to maximum concentration describes when the observed peak occurs; the elimination rate constant and apparent terminal half-life characterize the later decline in concentration. They complement the peak concentration outcome, but they do not substitute for an overall exposure measure or for a formal bioequivalence analysis. The registry record’s outcome descriptions do not state prespecified decision thresholds for these secondary measures.

The secondary results carry less inferential weight because they are not identified as the primary endpoint, the registry lists no sponsor-reported analyses, and no multiplicity strategy is reported. When several outcomes are examined, unadjusted p-values and intervals require cautious interpretation: the collection of results can produce apparently notable findings by chance, and selective emphasis can distort the overall picture. This is a general statistical concern, not an assertion about how the study team reported or selected results.

The useful conclusion from the secondary outcomes is therefore limited to their descriptive consistency with the primary summary. Their unadjusted results do not supply the missing formal criteria, paired analysis details, or sponsor-reported bioequivalence conclusion. They should be treated as context for the concentration profile rather than as separate proof that the products meet a regulatory or clinical equivalence standard.

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

• Time to Maximum Concentration (Tmax)
• Terminal Elimination Rate Constant (λz)
• Apparent Terminal Elimination Half-Life (t½)

9. Statistical Interpretation

10. Statistical Methods Explained

The main statistical distinction in this study is between a descriptive comparison of posted summaries and a formal analysis designed for a randomized crossover trial. The registry supplies group means and standard deviations for the outcomes. The accompanying unadjusted comparisons use those summaries to describe the difference between the test and reference groups. They do not provide the participant-level information needed to reconstruct every feature of a crossover analysis.

What does a mean and standard deviation describe?

A mean is the arithmetic average of the measured values in a group. It gives a measure of the group’s central location but does not show how much individual values vary. The standard deviation describes the spread of observations around that average. A large standard deviation relative to the mean difference can make a comparison imprecise, while a smaller spread can make the same difference easier to estimate. These are general statistical concepts; they do not, on their own, determine whether formulations meet a bioequivalence standard.

The registry reports Cmax as a mean with standard deviation. It also reports the same type of summary for the secondary continuous outcomes. Such summaries can help readers see the observed scale and variability, but they omit the individual-level pairing that is central to a crossover design. In that design, the two treatment measurements from a participant are related rather than independent. A paired analysis can use that relationship when estimating the treatment contrast.

What does the posted mean difference represent?

The Cmax comparison is stated as the test product minus the reference product. Its estimate is -0.038, and its 95% confidence interval runs from -0.258 to 0.181. The estimate is a simple unadjusted contrast based on the posted summaries. Its sign indicates the direction of the observed contrast as defined; it should not be read as a treatment effect adjusted for the crossover design unless the registry reports such an analysis. The record lists no reported analyses, and it does not identify this contrast as the sponsor’s formal result.

A confidence interval describes a range of estimates compatible with the data and the method used to construct the interval. It is not a range containing a guaranteed proportion of individual participant results, and it is not the probability that the true effect lies inside the particular interval. For a conventional difference interval, an interval containing zero indicates that a zero difference remains compatible with that calculation. It does not establish equivalence, because equivalence requires comparing the interval with prespecified bounds that define acceptable similarity.

Why does the crossover structure matter?

In a crossover trial, each participant’s results across treatment periods can be correlated. The degree of within-participant correlation affects the standard error of a paired treatment contrast. Separate group means and standard deviations do not reveal that correlation. Thus, a summary-statistic contrast that treats groups as separate may not reproduce the precision or inference of a paired model. The registry record does not report the sponsor’s model, treatment sequence allocation, period effects, carryover handling, or a formal analysis population. Those elements are not recoverable from the posted summaries alone.

Randomization of treatment order helps guard against systematic differences in the sequence assigned, while the crossover structure lets participants serve as their own comparison. These are general design features, not proof that all potential biases were avoided. Interpretation also depends on implementation details, such as whether participants completed both periods and whether the interval between treatments was sufficient to address carryover. Those details are not reported in the registry record.

Why is a nonsignificant p-value not proof of equivalence?

A p-value for a difference test summarizes how inconsistent the observed data are with a specified null hypothesis under the assumed analysis. The Cmax unadjusted p-value is 0.734. This does not give the probability that the treatments are equal, and it does not measure the probability that a bioequivalence criterion has been met. A conventional difference test may fail to reject a zero-difference hypothesis when estimates are imprecise, even when the data do not demonstrate that the difference lies within acceptable limits.

Formal bioequivalence methods require an explicit definition of the acceptable range and an analysis aligned with that objective. The registry record does not report the acceptance limits, the planned transformations, or the formal testing procedure. No conclusion about a formal bioequivalence test can therefore be reconstructed from the listed p-value alone. This is a general distinction between testing for a difference and evaluating equivalence, applied to the information absent from this particular record.

How should the secondary outcomes be handled?

The secondary outcomes are time to maximum concentration, terminal elimination rate constant, and apparent terminal elimination half-life. Each is reported as a continuous measure with a group mean and standard deviation. Their posted unadjusted comparisons describe differences in those measures, but the registry does not list sponsor-reported analyses for them. The results are useful as supporting descriptive information about the concentration-time profile, not as independent confirmation of the primary bioequivalence question.

When several outcomes are tested, the chance of observing at least one apparently unusual result can increase if each is interpreted using an unadjusted threshold. Methods for controlling multiplicity can address that issue, but the registry record does not report a multiplicity strategy. The record also does not state whether the secondary analyses were confirmatory or exploratory. These are general considerations, not claims that a particular adjustment was or was not used beyond what is documented.

What does over-dispersion mean in general?

For count outcomes, over-dispersion means that the observed variability exceeds what a simple model assumes. It can make standard errors too small if ignored. This study’s listed pharmacokinetic outcomes are continuous measures, and the registry record does not identify an over-dispersion analysis. The concept is therefore not a specific finding from this trial; it is a general example of why model assumptions should match the outcome and data structure.

For this record, the central methods limitation is not evidence of a particular model failure. It is the absence of the sponsor’s reported statistical method and formal bioequivalence criteria. The posted statistics support a descriptive reading and simple unadjusted recalculations, while leaving the planned inferential approach not reported in the registry record.

11. Confidence Intervals and Precision

Precision is reflected in the width of a confidence interval: narrower intervals indicate a more tightly estimated contrast under the method used, while wider intervals leave a broader range of values compatible with the data. The Cmax unadjusted estimate is -0.038, with a 95% confidence interval from -0.258 to 0.181. Because the interval spans zero, the calculation does not clearly distinguish a difference from no difference. At the same time, the interval extends in both directions, so it does not show that all plausible differences are negligible.

The p-value of 0.734 is consistent with the interval’s failure to exclude zero in this unadjusted comparison. Neither statistic supplies a probability that the treatments are identical. More importantly for the stated objective, the confidence interval cannot be judged against bioequivalence limits because those limits are not reported in the registry record. Precision relative to a decision threshold can only be evaluated when that threshold and the planned analysis are known.

The interval is based on a simple unadjusted comparison of posted summary statistics. In a crossover study, a paired analysis may have different precision because it uses the association between measurements within a participant. The registry does not report the paired treatment contrast or its confidence interval. Therefore, the posted interval is informative about the summary-statistic comparison, but it may not represent the precision of the sponsor’s intended crossover analysis.

The secondary confidence intervals likewise include zero, but they should not be treated as evidence of exact equality. Their precision must also be interpreted in light of the unreported analysis plan and the absence of a stated multiplicity approach. Without the formal criteria and model details, the registry supports a limited conclusion: the unadjusted estimates do not show a clear difference, but the precision and decision relevance for formal bioequivalence remain uncertain.

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 illustrations translate an observed effect into hypothetical sample-size requirements under stated assumptions. These figures are participants per arm, not total participants and not total events. The study’s own original sample-size assumptions are not reported in the registry record. The illustrations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect.

The 80% power column describes the planned chance of detecting the specified effect under those assumptions if that effect is real; the 90% power column uses a higher target chance of detection. These are planning concepts, not guarantees about the outcome of a future study. For instance, planning for 75% of the observed effect gives 3,861 participants per arm for 80% power and 5,169 participants per arm for 90% power. Planning for 50% of the observed effect gives 8,687 participants per arm for 80% power and 11,630 participants per arm for 90% power. Smaller effects need more participants to detect under the same assumptions.

The figures are illustrations derived from the observed effect, rather than a reconstruction of the crossover study’s original design. They do not incorporate a paired crossover correlation in the assumptions stated, and the posted record does not report enough information to assess how the illustrations relate to a formal paired design. The sample-size figures are not observed power. They should be read as hypothetical planning quantities under the listed assumptions, not as an explanation of the completed study’s design or a measure of how likely its findings were to be correct.

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 = -0.038; pooled standard deviation σ = 0.448.
2. n = 2 × (1.96 + 0.842)² × 0.448² / -0.038² = 2,171.7, rounded up to 2,172 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 <- -0.0381                      # observed difference in means
sigma <- 0.44813157108153                     # 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(4411940)
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 = 2,172 (80% power), 2,908 (90% power)
 75% of observed effect: n per arm = 3,861 (80% power), 5,169 (90% power)
 50% of observed effect: n per arm = 8,687 (80% power), 11,630 (90% power)
power.t.test: 2172.7 
Simulated power at n = 2,172 per arm: 0.801 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity concerns arise when a study evaluates multiple outcomes or makes multiple statistical comparisons. If each is tested without adjustment, the overall chance of at least one result appearing statistically unusual can be greater than the chance associated with an individual test. This matters especially when secondary outcomes are interpreted alongside a primary endpoint. A prespecified hierarchy or adjustment can help clarify which findings are confirmatory and how the family of tests should be interpreted.

The registry record lists a primary Cmax outcome and three secondary pharmacokinetic outcomes. It does not report a multiplicity strategy, an outcome hierarchy beyond identifying the primary endpoint, or whether the secondary analyses were confirmatory. The posted comparisons are unadjusted. Their p-values should therefore not be read as if the record documented a family-wise interpretation or an adjustment for multiple testing.

Missing-data handling is also not reported in the registry record. The outcome summaries show 32 observations for each treatment, but the record does not describe whether any measurements were missing, how incomplete treatment periods were handled, or whether analyses used all randomized participants or a subset. A displayed group count does not by itself answer those questions, particularly for a crossover study where complete data across periods can matter for a paired comparison.

The analysis populations are not defined in the record. It does not report an intention-to-treat, per-protocol, pharmacokinetic, or safety population definition. Nor does it explain exclusions, deviations, or evaluability rules. Such definitions can affect which participants contribute to the formal bioequivalence analysis and how results should be interpreted.

The registry lists no reported analyses. Consequently, the planned statistical model, handling of period and sequence, treatment of carryover, missing-data assumptions, and multiplicity procedures are not reported in the registry record. These are gaps in the accessible record, not evidence that the trial team did not address them in the protocol or another analysis document. Without those details, the posted summaries can be described, but the prespecified inferential framework cannot be fully assessed.

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 the reference treatment group and zero in the test treatment group. The number at risk for serious adverse events is reported as 32 in each group. The record also reports zero deaths in each group. These figures indicate that no serious adverse events or deaths were recorded in the posted group summaries.

For other, non-serious adverse events, the registry reports 26 affected participants in each treatment group, with 32 at risk in each. Those counts are descriptive. They do not show whether the same types of events occurred, how often events recurred, when they occurred, or how severe they were. The posted safety summary does not identify the event terms.

These group counts do not establish that the formulations have equivalent safety profiles. The trial is a single-dose study in healthy participants, and the record does not report a formal comparative safety analysis or detailed event listings in the information available. Safety interpretation should remain limited to the event counts recorded in the registry.

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

The posted results describe a randomized crossover comparison of two haloperidol tablet formulations under fasting conditions. The primary Cmax group summaries are similar, and the unadjusted summary-statistic contrast has a confidence interval that includes zero. The secondary unadjusted comparisons also have intervals that include zero. In ordinary terms, these calculations do not show a clear difference between the posted treatment summaries.

That is a narrower conclusion than saying the formulations are bioequivalent. Failure to detect a difference is not proof that any difference is small enough to meet an equivalence standard. A formal bioequivalence conclusion requires stated acceptance limits and an analysis appropriate to the objective. The registry record does not report those limits or the sponsor’s formal analysis, so the record does not establish whether the study met its stated bioequivalence objective.

The summary-statistic comparisons are unadjusted and do not show how the crossover pairing was handled. Separate means and standard deviations cannot reproduce the within-participant association. The record also does not report the randomized treatment sequences, washout details, missing-data approach, analysis populations, or multiplicity plan. These omissions limit how much can be inferred about precision and the planned analysis.

The study does not address clinical effectiveness in patients. It enrolled healthy males and females and measured pharmacokinetic outcomes after a single dose under fasting conditions. The listed results therefore do not establish how the formulations compare in other populations, dosing conditions, repeated use, or clinical outcomes.

The safety counts show no serious adverse events or deaths in the posted summaries and report other adverse events in both groups. These counts are not a comprehensive comparative safety assessment and should not be treated as evidence that the treatments have identical safety profiles.

The most appropriate interpretation is descriptive: observed group summaries and simple unadjusted contrasts are broadly similar, but the formal bioequivalence conclusion, its uncertainty under the crossover analysis, and the protocol’s decision criteria are not reported in the registry record.

17. Why This Trial Matters Statistically

This trial is statistically instructive because it combines a common bioequivalence objective with a crossover design. A crossover can be efficient for comparing pharmacokinetic measurements when within-participant comparisons are informative. At the same time, that design makes the analysis structure important: the treatment measurements are paired, and the correlation between them can affect the estimated uncertainty. A reader cannot recover that feature from separate treatment means and standard deviations alone.

The record also illustrates why a non-significant difference test is not interchangeable with an equivalence test. The Cmax unadjusted comparison has a p-value of 0.734, but that p-value addresses a conventional difference question under its calculation. Bioequivalence requires judging uncertainty against prespecified acceptance criteria. Without those criteria and the formal sponsor analysis, similar observed means are not enough to reconstruct a bioequivalence decision.

Another lesson is the distinction between an observed-effect planning illustration and a trial’s original design justification. The registry includes hypothetical planning quantities based on fractions of the observed effect and stated assumptions. These figures can help readers understand how detectable effects relate to sample-size planning, but they do not tell why the study enrolled its reported number of participants. The original justification is not reported in the registry record.

Finally, the record demonstrates the value of complete statistical reporting. Analysis populations, handling of missing data, treatment sequence and period effects, multiplicity plans, and formal outcome analyses all affect interpretation. Their absence from the registry does not prove they were absent from the study documentation; it does mean that the publicly recorded summaries support a more limited statistical assessment than a full protocol and analysis report would allow.

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 trial-specific limitation is that the registry record does not report the formal bioequivalence criteria or sponsor-reported analysis. The posted Cmax and secondary comparisons are unadjusted summary-statistic calculations, and the record lists no reported analyses. It is therefore not possible to verify the formal decision method or confirm whether it accounted for the crossover structure.

The record identifies a randomized, two-period crossover design but does not describe treatment sequence allocation, washout duration, period effects, or carryover handling. It also does not report participant-level paired results, so the within-person correlation and the precision of a paired treatment contrast cannot be assessed from the posted group summaries.

Other analysis details are not reported in the registry record: the analysis populations, exclusions, missing-data handling, multiplicity approach, and whether the secondary outcomes were confirmatory. These omissions limit assessment of the analysis plan and the robustness of the results. The record also does not report the original sample-size rationale or assumptions, so the planning illustrations should not be mistaken for that rationale.

The study population and conditions are specific: healthy males and females, fasting conditions, and a single dose. The results do not directly describe other populations or dosing settings. The safety summary is also limited to event counts; detailed event terms and a formal comparative safety analysis are not reported in the information available.

Finally, the primary posted outcome is Cmax. The record’s outcome descriptions do not report an area-under-the-curve endpoint, which would provide a different view of exposure over time. This analysis therefore cannot assess that aspect of pharmacokinetic similarity from the outcomes described in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Bioequivalence Study of Two Oral Haloperidol Tablets Formulations in Healthy Subjects Under Fasting Conditions — NCT04411940.
• Registry record last updated 2022-06-08; status last verified 2022-03.
• Results first posted 2022-06-08.
• 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 identifies NCT04411940 as a completed phase 1, randomized, open-label, single-center, single-dose, two-period crossover study of two haloperidol 2 mg tablet formulations in healthy males and females under fasting conditions. Enrollment was 32, and the listed dates are 2019-11-15 for study start and 2019-12-18 for primary completion.

The primary outcome was mean Cmax, the maximum observed plasma concentration of haloperidol. Three secondary outcomes were listed: time to maximum concentration, terminal elimination rate constant, and apparent terminal elimination half-life. Posted group summaries and unadjusted comparisons show no clear differences, but the formal sponsor analyses and bioequivalence criteria are not reported in the registry record.

The safety summary reports zero serious adverse events and zero deaths in each treatment group, and 26 participants with other adverse events in each group. These counts are descriptive and do not establish comparative safety or formal bioequivalence.