Bioequivalence Between Albuterol Sulfate Inhalation Aerosol 108 mcg Per Actuation and Proair HFA (Albuterol Sulfate) Inhalation Aerosol 90 mcg Per Actuation in Healthy Volunteers Under Fasting Conditions: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Bioequivalence Between Albuterol Sulfate Inhalation Aerosol 108 mcg Per Actuation and Proair HFA (Albuterol Sulfate) Inhalation Aerosol 90 mcg Per Actuation in Healthy Volunteers Under Fasting Conditions (NCT04803734), a randomized na study. The primary outcome is Cmax.

2. Clinical Question

The clinical question is pharmacokinetic rather than a test of symptom relief or clinical benefit. The registry describes a comparison of drug exposure after a single dose in healthy volunteers, not treatment outcomes in people with a health condition. The trial title and summary specify fasting conditions, and the two products are described as having the same equivalent Albuterol amount per puff despite different stated amounts of Albuterol Sulfate per actuation. Whether all stated exposure measures met the criterion cannot be determined from the posted primary result alone: the reported analysis available for interpretation is the Cmax ratio, while the registry’s Cmax endpoint is reported separately as arithmetic means and standard deviations.

3. Trial Design

NCT04803734 is a completed, randomized, single-dose, open-label, two-way crossover study sponsored by Intech Biopharm Ltd. The registry lists healthy volunteers as the population and fasting conditions as the study setting. The study start date is 2021-03-19, and primary completion is dated 2021-05-10. The phase is listed as NA.

A crossover design compares treatments within participants across treatment periods rather than assigning each participant to only one treatment throughout the study. That general design can reduce the influence of stable differences between participants on treatment comparisons. The registry identifies the study as a two-way crossover and lists a test and a reference product. The specific treatment sequences, period length, washout duration, and details of crossover implementation are not reported in the registry record. Randomization is reported, but the randomization procedure and allocation concealment are not reported in the registry record.

Masking is listed as none, so the study is open-label. The registry reports enrollment of 60 participants. The primary endpoint’s population description states that data from 53 subjects were considered for pharmacokinetic and statistical analysis. It notes protocol issues for R014, R040, R055, and R058, including significantly delayed blood sampling and leakage of drug during dosing. It also notes pre-dose concentrations greater than 5% of Cmax for R029 and R058. The record does not explain in detail how these reasons were applied across the analysis populations, including how the overlapping mention of R058 was handled.

The primary endpoint is Cmax, with measurements scheduled from pre-dose through 24 hours post-dose. The registry lists secondary outcomes of Tmax, T1/2, Kel(λ), and Mean Residence Time (MRT). The analysis population and study design are relevant to interpreting the estimates: the findings concern the analyzed healthy volunteers and the conditions of this particular single-dose comparison, not all patient groups or dosing settings.

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: Sixty eligible subjects were randomized in the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: R014, R040, R055, R058 had protocol issues including significantly delayed blood sampling and leakage of drug during dosing. R029 and R058 had pre-dose concentrations \> 5% of Cmax. Data of remaining 53 subjects was considered for pharmacokinetic and statistical analysis.

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, measured over 0 hour (pre-dose), as well as at 2, 5, 10, 15, 20, 30, 45 minutes, and 1, 1.25, 1.5, 1.75, 2, 2.25, 2.5, 3, 4, 6, 8, 12, 16 and 24 hours post-dose.

Cmax is the maximal observed plasma concentration of Albuterol Sulfate after dosing. It describes the highest measured concentration during the sampling period, rather than the total amount of drug exposure over time. The registry lists Cmax in pg/mL as the primary endpoint and gives a sampling schedule that begins at 0 hour (pre-dose), includes multiple early post-dose time points, and continues through 24 hours post-dose.

As a general pharmacokinetic concept, Cmax is used to characterize the peak concentration reached after a dose. In a bioequivalence comparison, a treatment-to-reference estimate for Cmax helps assess whether the products produce sufficiently similar peak exposure under the study conditions. The registry states a bioequivalence range of 80.00-125.00% for the ln-transformed Cmax ratio, along with AUC(0-t) and AUC(0-inf). The reported primary analysis gives a geometric least-square-mean ratio and its 90% confidence interval. This ratio-based analysis is the relevant form for comparison against the stated bioequivalence range; the posted arithmetic means and standard deviations describe the endpoint but do not by themselves express the registry’s formal ratio-based bioequivalence result.

The interpretation remains specific to the endpoint and sampling conditions. A measured maximum can depend on how sampling is timed, which makes the registry’s mention of delayed blood sampling pertinent. Cmax alone does not summarize the full concentration-time profile, and it does not establish a clinical effect. AUC measures, the other exposure measures named in the criterion, are not detailed in the posted primary result. Their numerical estimates and confidence intervals are not reported in the registry record.

7. Results Posted in the Registry

• Proair HFA (Albuterol Sulfate) Inhalation Aerosol: mean 945.46 versus 812.48 on control; difference 132.98 (95% CI 10.07 to 255.89), standardized effect d = 0.41; z-test p = 0.034.

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.

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:
  • Proair HFA (Albuterol Sulfate) Inhalation Aerosol: mean 0.51 versus 0.93 on control; difference -0.42 (95% CI -0.74 to -0.09), standardized effect d = -0.48; z-test p = 0.013.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Proair HFA (Albuterol Sulfate) Inhalation Aerosol than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

T1/2

• 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:
  • Proair HFA (Albuterol Sulfate) Inhalation Aerosol: mean 6.99 versus 6.93 on control; difference 0.06 (95% CI -0.42 to 0.54), standardized effect d = 0.05; z-test p = 0.817.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Proair HFA (Albuterol Sulfate) Inhalation Aerosol and the control. The interval gives the range of effects that remain compatible with the data.

Kel(λ)

• 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:
  • Proair HFA (Albuterol Sulfate) Inhalation Aerosol: mean 0.10 versus 0.10 on control; difference 0.00 (95% CI -0.01 to 0.01), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Proair HFA (Albuterol Sulfate) Inhalation Aerosol and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists Tmax, T1/2, Kel(λ), and Mean Residence Time (MRT) as secondary outcomes. Numerical summaries are posted for Tmax, T1/2, and Kel(λ); a numerical result for Mean Residence Time is not reported in the registry record. Across the posted secondary measures, the pattern is not one of uniformly aligned differences: the descriptive contrasts vary in direction and size, and their uncertainty differs. These outcomes provide additional pharmacokinetic context but do not replace the primary Cmax bioequivalence result.

The primary result addresses the stated Cmax ratio criterion. Secondary outcomes characterize other features of the concentration-time profile, such as timing of the maximum concentration and elimination-related measures. As general statistical context, secondary endpoints can help describe whether a treatment comparison is consistent across related measures, but they may be exploratory or supportive rather than the main basis for a trial’s principal conclusion. The registry record does not report a hierarchy of endpoint testing or identify which secondary comparisons, if any, were confirmatory.

The posted secondary comparison p-values are unadjusted. When several endpoints are tested, the chance of at least one apparently notable result can increase if multiplicity is not accounted for. This general concern means an isolated unadjusted secondary p-value should be interpreted cautiously, especially without a declared testing hierarchy or multiplicity procedure. Such results describe observed contrasts and uncertainty, but they carry less weight than the stated primary endpoint and its formal bioequivalence analysis.

The record reports three analyses in the primary outcome data and lists four secondary outcomes, while numerical summaries are available for only three secondary measures. The reason the MRT result is absent, and whether it was collected or analyzed, are not reported in the registry record. Nor are detailed secondary analysis methods or multiplicity adjustments reported. The overall secondary pattern is therefore useful for context, but it cannot establish a complete, prespecified picture of all secondary pharmacokinetic outcomes.

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

• Tmax
• T1/2
• Kel(λ)
• Mean Residence Time (MRT)

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports an ANOVA for the primary Cmax bioequivalence analysis, with the result expressed as a ratio of geometric least-square means. It also posts descriptive means and standard deviations on the original pg/mL scale. These statistics should not be treated as interchangeable: one is a model-based relative comparison, while the other summarizes the observed endpoint values by treatment.

What does a geometric least-square-mean ratio describe?

As a general statistical explanation, concentration data are often analyzed after logarithmic transformation because ratios are central to exposure comparisons and the transformed values may behave more suitably for model-based analysis. A geometric least-square mean is derived from a model on the transformed scale and then expressed on the original ratio scale. The estimate of 0.862 therefore describes the test-to-reference relation in relative terms, rather than a difference in pg/mL. The confidence interval for that ratio can be compared with the stated bioequivalence limits of 80.00-125.00%.

The registry says the test-to-reference ln-transformed AUC(0-t), AUC(0-inf), and Cmax were to be assessed against that range. The reported primary ANOVA result is for Cmax. Details such as the full model specification, included effects, handling of treatment periods and sequences, and exact transformation and estimation procedures are not reported in the registry record. The design is crossover, but the record does not describe the model terms used to reflect that structure.

Why are two kinds of Cmax summaries posted?

The arithmetic means and standard deviations describe Cmax in its original units. The test-group mean is 812.5 pg/mL with standard deviation 281.1, and the reference-group mean is 945.5 pg/mL with standard deviation 359.7. Each group summary is based on 53 participants. These statistics communicate the level and spread of observed values but do not reproduce the model-based ratio analysis. In particular, the arithmetic means do not encode all features of a crossover model or the geometric transformation used in the sponsor’s reported result.

A separate unadjusted re-calculation uses those posted summaries to estimate a mean difference and confidence interval. Such a calculation is a simple comparison on the arithmetic scale; it does not incorporate unreported subject-level data or model details. The record’s discrepancy flag is false, so there is no noted conflict requiring the sponsor’s analysis to take precedence over a discrepant re-calculation. Even so, the sponsor’s reported analysis remains the relevant result for interpreting the registry’s formal bioequivalence assessment, while the re-calculation provides a different, descriptive statistical perspective.

What does the confidence interval contribute?

As a general explanation, a confidence interval gives a range of values compatible with the data and the statistical model at the stated confidence level. It conveys uncertainty around an estimate and should be read together with the estimate’s scale and purpose. For bioequivalence, the important comparison is whether the full interval is contained within the stated acceptance limits, not merely whether a test of no difference gives a small p-value. The primary reported 90% interval runs from 0.807 to 0.922 and is within the listed 80.00-125.00% range.

The re-calculated mean difference has a 95% interval from 10.07 to 255.9 pg/mL. That interval concerns an absolute difference, not a test-to-reference ratio. Its p-value of 0.034 is an unadjusted test of a difference between arithmetic means, so it should not be used as a substitute for the ratio-based bioequivalence assessment. The reported ANOVA p-value is 0.033, but a p-value alone does not establish bioequivalence; the interval relative to the margins carries the direct interpretation.

What assumptions and analysis details remain unclear?

General statistical interpretation depends on the study’s analysis population, measurement quality, and modeling choices. The record identifies 53 participants for pharmacokinetic and statistical analysis and describes protocol issues affecting sampling or dosing. It does not provide a full participant disposition, treatment sequence counts, missing-data methods, sensitivity analyses, or the sponsor’s detailed rationale for the analysis population. The original sample-size justification, interim analysis plan, and complete statistical analysis plan are not reported in the registry record. These gaps limit independent assessment of model adequacy and robustness, even though the reported primary estimate and confidence interval can still be described as posted.

11. Confidence Intervals and Precision

The sponsor-reported primary Cmax ratio is 0.862, with a 90% confidence interval from 0.807 to 0.922. In bioequivalence analysis, the interval’s position relative to the stated limits is important: the full reported interval falls within 80.00-125.00%. This communicates both the estimated relative exposure and the uncertainty around it under the reported analysis. It is more informative for the bioequivalence question than the point estimate alone, because an estimate by itself does not show how much uncertainty surrounds it.

As a general statistical explanation, a confidence interval is not a guarantee that the true value lies within that particular interval, nor does it show the range of individual participant responses. It reflects uncertainty in an estimated population-level quantity under the analysis assumptions. Here the reported interval concerns a geometric least-square-mean ratio for Cmax, not the arithmetic mean difference and not the full distribution of Cmax measurements.

The unadjusted re-calculation gives a mean difference of 133.0 pg/mL, with a 95% confidence interval from 10.07 to 255.9. That interval is on a different scale and answers a different question from the sponsor’s ratio interval. Its width reflects uncertainty in the arithmetic-scale difference using the posted summary statistics; it should not be compared directly with the bioequivalence margins. The sponsor’s analysis and the re-calculation are not discordant analyses of the exact same estimand.

Precision is also tied to which participants were analyzed and whether the sampling schedule captured peak concentrations reliably. The record states that data from 53 subjects were considered, and it notes delayed blood sampling and dosing leakage among protocol issues. It does not report sensitivity analyses addressing those concerns. Thus, the confidence interval is precise in the statistical sense of the reported model and data, but does not resolve uncertainty about the consequences of protocol deviations or broader applicability to other populations and dosing conditions.

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 illustrations based on the observed effect, not the trial’s original sample-size design. They assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to a stated fraction of the observed effect. For the continuous outcomes in this study, the counts are participants per arm, not total events. The time-to-event convention does not apply to these outcomes.

The 80% power column means the illustrated sample size per arm under which a study would have an 80% chance of detecting the specified effect if the assumptions were met. The 90% power column gives the corresponding illustration for a 90% chance. These are planning quantities under the stated model assumptions; they are not a retrospective statement about the chance that this completed trial detected an effect. This is not observed power.

The planning rows vary the effect size relative to the observed effect: 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The smaller the effect targeted for detection, the more participants per arm the illustration requires. For example, for Cmax, planning for 100% of the observed effect gives 93 participants per arm for 80% power and 124 participants per arm for 90% power; planning for 50% gives 371 and 496, respectively. These are examples of the relationship between a smaller target effect and a larger planning sample, not recommendations for a future study.

The registry’s original sample-size justification and design assumptions are not reported in the registry record. The observed-effect illustrations should therefore not be used to infer why 60 participants were enrolled, whether the trial was originally powered for a particular endpoint, or whether the achieved analysis population met a planned target. The same caveat applies to planning figures for secondary outcomes: they are based on observed comparisons and do not establish a prespecified design rationale.

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 = 132.979; pooled standard deviation σ = 322.819.
2. n = 2 × (1.96 + 0.842)² × 322.819² / 132.979² = 92.5, rounded up to 93 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 <- 132.979                      # observed difference in means
sigma <- 322.819369717029                     # 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(4803734)
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 = 93 (80% power), 124 (90% power)
 75% of observed effect: n per arm = 165 (80% power), 221 (90% power)
 50% of observed effect: n per arm = 371 (80% power), 496 (90% power)
power.t.test: 93.5 
Simulated power at n = 93 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 sponsor’s reported primary analysis is the ANOVA estimate of the geometric least-square-mean ratio for Cmax: 0.862, with a 90% confidence interval from 0.807 to 0.922 and p = 0.033. The interval is within the stated bioequivalence range of 80.00-125.00%. This is the analysis that directly corresponds to the registry’s ratio-based bioequivalence criterion for Cmax.

The separate recalculated comparison uses the posted arithmetic means and standard deviations. It estimates a mean difference of 133.0 pg/mL, with a 95% confidence interval from 10.07 to 255.9 and p = 0.034. It is unadjusted and is not a reconstruction of the sponsor’s crossover ANOVA. The arithmetic-scale difference and the model-based ratio have different estimands, scales, and interval interpretations. Their point estimates and p-values should not be compared as if they were competing estimates of one identical quantity.

The record marks the discrepancy status as false, so no conflict between the posted sponsor analysis and the recalculation is flagged. The recalculation is useful as a transparent descriptive check, but the sponsor’s own analysis takes precedence for the formal bioequivalence question because it is the reported analysis framed around the stated ratio criterion. The numerical AUC analyses named in the study summary are not reported in the registry record, so the available sponsor result should not be extended to those measures.

15. Multiplicity, Missing Data and Analysis Populations

The registry describes a primary endpoint and several secondary pharmacokinetic outcomes. The study summary names AUC(0-t), AUC(0-inf), and Cmax as measures to be assessed against the bioequivalence range, while the posted primary endpoint is Cmax. The registry also lists Tmax, T1/2, Kel(λ), and Mean Residence Time (MRT) as secondary outcomes. A hierarchy among these outcomes, a plan for controlling multiplicity, or an explanation of how the bioequivalence decisions across the named exposure measures were combined is not reported in the registry record.

As a general statistical point, testing multiple outcomes can increase the chance of false-positive findings if each is interpreted independently without adjustment or a prespecified hierarchy. This is particularly relevant to secondary analyses whose reported p-values are unadjusted. The record does not state whether a multiplicity procedure was used. Without that information, secondary p-values should be viewed as descriptive evidence rather than as definitive independent claims.

Participant handling raises a separate interpretive issue. Enrollment was 60, and the endpoint population description says data from 53 subjects were considered for pharmacokinetic and statistical analysis. It identifies four participants with protocol issues, including delayed blood sampling and leakage of drug during dosing, and two participants with pre-dose concentrations greater than 5% of Cmax; R058 appears in both descriptions. Detailed reasons for every participant’s inclusion or exclusion, participant flow by treatment sequence, and the analysis populations used for the sponsor’s formal result are not reported in the registry record.

The registry does not describe methods for missing observations, handling of incomplete crossover data, sensitivity analyses, or how protocol deviations affected each endpoint. It also does not report the full statistical analysis plan, the original sample-size justification, or interim analysis details. These omissions do not invalidate the posted estimates, but they constrain independent evaluation of whether the analysis decisions were prespecified and whether results are robust to alternative choices. Interpretation should distinguish the reported Cmax estimate from questions about missing data, multiple testing, and analysis-population sensitivity that cannot be resolved from the registry record.

16. 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 serious adverse event counts are zero in both listed groups: 0 of 60 participants at risk in the Test Group and 0 of 58 participants at risk in the Reference Group. No deaths are reported in either group. These figures describe the registry’s serious-event counts during the recorded study; they do not mean that no non-serious adverse events occurred.

The registry lists other, non-serious adverse events for 4 of 60 participants at risk in the Test Group and 1 of 58 at risk in the Reference Group. The record does not provide the event terms in the posted summary, so their nature, severity, timing, and attribution cannot be described from these counts. The at-risk denominators differ between groups, and the record does not explain that difference in the adverse-event summary.

As a general interpretation principle, event counts from a small, short, single-dose study are descriptive and have limited ability to characterize uncommon or delayed events. This study was conducted in healthy volunteers under fasting conditions, and the safety figures should be understood in that setting. They do not establish comparative safety across broader patient populations or repeated dosing. The registry’s zero serious-event counts should be read narrowly as the recorded counts, not as evidence that serious events are impossible or that the products have identical safety profiles.

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

The posted Cmax analysis estimates a test-to-reference geometric least-square-mean ratio of 0.862, with a 90% confidence interval from 0.807 to 0.922. The interval is within the registry’s stated bioequivalence limits of 80.00-125.00%. Thus, the primary reported Cmax result is compatible with the stated criterion under the reported analysis. The sponsor-reported ratio analysis is the relevant result for that question; the unadjusted arithmetic mean difference is a distinct comparison on a different scale.

This finding does not establish that the two products have identical concentrations in every participant, or that every pharmacokinetic endpoint is the same. It does not describe clinical effectiveness, symptom relief, or outcomes in patients. The study assessed a single dose in healthy volunteers under fasting conditions, and its primary endpoint was a measured plasma concentration. Generalizing beyond those conditions requires evidence not contained in this registry result.

The study summary names AUC(0-t) and AUC(0-inf), as well as Cmax, in the bioequivalence criterion. However, numerical AUC results and confidence intervals are not reported in the registry record. Consequently, the Cmax interval should not be taken as a complete account of all exposure measures named in the summary. The record also lists secondary pharmacokinetic measures, but does not provide a numerical result for MRT.

The analysis population is another boundary on interpretation. Although 60 participants were enrolled, the primary endpoint description says that data from 53 subjects were considered for pharmacokinetic and statistical analysis. The listed protocol issues include delayed blood sampling, dosing leakage, and elevated pre-dose concentrations. The available summary does not provide enough detail to assess the effect of those issues on the result or on alternative analysis populations.

In short, the primary posted result supports a narrow statistical statement about Cmax in the analyzed population under this study’s conditions. It should not be converted into a broader claim about clinical benefit, all exposure measures, all dosing settings, or all populations.

18. Why This Trial Matters Statistically

This trial illustrates why bioequivalence analysis is not simply a test for whether two observed means differ. Its primary result is expressed as a ratio of geometric least-square means and judged against a defined range, 80.00-125.00%. The reported 90% confidence interval from 0.807 to 0.922 is interpreted in relation to those margins. That interval-based approach makes the decision question explicit: whether the plausible relative exposure values under the analysis remain within the stated bounds.

The registry also makes it possible to contrast the formal ratio analysis with a simple unadjusted arithmetic-scale re-calculation. These summaries are not contradictory merely because they have different values or p-values; they address different estimands. This is a useful statistical distinction for clinical researchers reviewing posted results: a test of no difference is not the same as an assessment of whether a treatment ratio is sufficiently close within prespecified limits.

The study also emphasizes the importance of analysis populations and measurement quality in pharmacokinetic research. The endpoint description notes delayed blood sampling and leakage of drug during dosing, as well as pre-dose concentrations for some participants. These details matter because concentration-time measures depend on valid dosing and correctly timed sampling. At the same time, the record’s limited participant-flow and sensitivity-analysis information makes it difficult to assess the robustness of the result to those issues.

Finally, the record demonstrates the boundary between a focused primary finding and a broader evidence claim. The Cmax analysis is reported with an interval suitable for the stated criterion, while numerical results for the AUC measures named in the summary are not reported in the registry record. A careful reading separates what the primary estimate directly addresses from what remains unavailable. This is central to transparent statistical interpretation: conclusions should follow the reported estimand, population, and precision, without extending beyond them.

19. 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 are specific to this study record. First, the study involved healthy volunteers under fasting conditions and a single dose. The results therefore concern that setting and do not directly represent other populations, feeding conditions, or dosing patterns. The registry does not provide further demographic characteristics or eligibility details in the posted summary.

Second, 60 participants were enrolled, while the primary endpoint description states that 53 subjects were included for pharmacokinetic and statistical analysis. It identifies protocol problems involving delayed blood sampling and leakage of drug during dosing, as well as pre-dose concentrations greater than 5% of Cmax. Detailed disposition, the handling of the participant named in both issue descriptions, and sensitivity analyses are not reported in the registry record. The effect of these issues on the primary estimate cannot therefore be assessed independently from the summary.

Third, the reported bioequivalence analysis is available for Cmax, while the study summary names AUC(0-t) and AUC(0-inf) as additional measures in the criterion. Their numerical estimates and confidence intervals are not reported in the registry record. Mean Residence Time is listed as a secondary outcome but its numerical result is also not reported. This limits assessment of the full pharmacokinetic profile.

Fourth, the registry does not report the complete statistical model, treatment sequence details, washout duration, multiplicity strategy, missing-data approach, original sample-size justification, interim analysis plan, or sensitivity analyses. The study is identified as randomized and crossover, but those labels alone do not resolve how period and sequence effects or incomplete data were handled. These limitations qualify independent appraisal of robustness and generalizability, without changing the fact that the posted Cmax interval is within the stated range.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Bioequivalence Between Albuterol Sulfate Inhalation Aerosol 108 mcg Per Actuation and Proair HFA (Albuterol Sulfate) Inhalation Aerosol 90 mcg Per Actuation in Healthy Volunteers Under Fasting Conditions — NCT04803734.
• Registry record last updated 2024-03-18; status last verified 2024-03.
• Results first posted 2023-09-25.
• 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.

23. Record Summary

NCT04803734 is a completed, randomized, open-label, single-dose, two-way crossover study sponsored by Intech Biopharm Ltd. It compared Albuterol Sulfate inhalation aerosol 108 mcg per actuation with Proair HFA (Albuterol Sulfate) inhalation aerosol 90 mcg per actuation in healthy volunteers under fasting conditions. Enrollment was 60, with data from 53 subjects considered for pharmacokinetic and statistical analysis.

The primary endpoint was Cmax. The sponsor-reported ratio of geometric least-square means was 0.862, with a 90% confidence interval from 0.807 to 0.922, within the stated 80.00-125.00% bioequivalence limits. Numerical AUC analyses named in the study summary are not reported in the registry record. The results describe the reported pharmacokinetic comparison and should be interpreted within its population, single-dose conditions, analysis details, and endpoint-specific limits.