Efficacy and Safety Study of BCX7353 as an Oral Treatment for the Prevention of Attacks in HAE: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety Study of BCX7353 as an Oral Treatment for the Prevention of Attacks in HAE (NCT03485911), a randomized phase 3 study. The primary outcome is Part 1: The Rate of Investigator-confirmed HAE Attacks During Dosing in the Entire 24-week Treatment Period (Day 1 to Day 168).

2. Clinical Question

3. Trial Design

The registry describes a Phase 3, multicenter, randomized, double-blind, placebo-controlled, parallel-group study. It lists triple masking and random allocation. The study was designed to evaluate the efficacy and safety of two dose levels of oral BCX7353 for prevention of attacks in people with hereditary angioedema. The brief summary specifies Type I and Type II HAE.

The registry reports enrollment of 121 and lists three primary-outcome groups: berotralstat 110 mg once daily, berotralstat 150 mg once daily, and placebo. The primary analysis population is described as all randomized subjects, regardless of whether they received study treatment. The outcome entries list 41, 40, and 40 subjects in those respective groups. These are the group counts shown for the primary outcome, not a substitute for details about the flow of participants through the study.

The primary endpoint covers the entire 24-week treatment period, from Day 1 to Day 168. Each active dose was compared with placebo; no active-dose-versus-active-dose primary comparison is reported. The record also lists secondary outcomes, including quality of life, days with angioedema symptoms, and expert-confirmed events. It describes Part 2 outcomes related to berotralstat over longer periods, but the primary result is the Part 1 attack-rate outcome.

The registry records the study as completed, with a start date of 2018-02-06 and a primary completion date of 2019-04-10. It does not report the rationale for the selected enrollment, the planned allocation ratio, or additional operational details beyond the design descriptions stated in the 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: Subjects with HAE Type 1 or Type 2 were eligible for the study following assessment of data obtained from screening procedures, including demonstration of a minimum number of qualifying HAE attacks documented during a prospective run-in period of 14 to 56 days from the date of the screening visit. Randomization was stratified by the HAE attack rate over the period between screening and randomization (≥ 2 attacks per month vs. \< 2 attacks per month).

Part 1

Reasons for not completing this period:

Part 2

Reasons for not completing this period:

Part 3

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The intent to treat (ITT) population included all randomized subjects, regardless of whether study treatment was administered. This population was the primary population for the analysis of the efficacy and health outcomes data.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Intent to treat population

6. Primary Endpoint

The registry lists the primary outcome as Part 1: The Rate of Investigator-confirmed HAE Attacks During Dosing in the Entire 24-week Treatment Period (Day 1 to Day 168), measured over 24 weeks.

The primary endpoint is the rate of investigator-confirmed HAE attacks during the entire 24-week dosing period, expressed as attacks per 28 days. It measures the frequency of confirmed attacks over time, rather than the proportion of participants who experienced at least one attack. The analysis population is the intent-to-treat population, defined in the registry as all randomized subjects regardless of whether study treatment was administered.

Attack rates are useful in a prevention trial because participants can have different amounts of time on treatment and different numbers of attacks. A rate expresses event frequency relative to time observed. The registry’s analysis accounts for duration on treatment through an offset and includes baseline attack rate as a covariate. These features reflect the stated model; they do not establish how missing observations or treatment discontinuation were handled.

For each group, the posted estimated rates are 1.65 for berotralstat 110 mg, 1.31 for berotralstat 150 mg, and 2.35 for placebo, all per 28 days. The reported treatment comparisons express the results as the attack-rate ratio of berotralstat over placebo, with a 95% confidence interval. A confidence interval communicates the uncertainty around the model-based comparison: narrower intervals indicate greater precision, while wider intervals indicate less precision. The interval should be read together with the point estimate and the reported p-value, not as a guarantee about the result in another study.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

Why use a negative binomial model?

The primary endpoint counts attacks, so a model for count data is appropriate in general. A simple count model may be inadequate when the observed counts vary more than the model expects. This extra variability is called over-dispersion. In general, a negative binomial model allows for more variation in counts than a Poisson model and can produce uncertainty estimates better matched to over-dispersed data. Whether over-dispersion was assessed, and what alternatives were considered, is not reported in the registry record.

The registry describes the number of investigator-confirmed attacks as the dependent variable, treatment as a fixed effect, baseline attack rate as a covariate, and the logarithm of duration on treatment as an offset. In general, an offset allows a count model to estimate a rate when observation time varies. The baseline-rate covariate incorporates the stated stratification variable into the model. These are the model components described in the record; further model diagnostics and implementation details are not reported.

What does the rate ratio express?

The reported treatment contrast is an attack-rate ratio, defined in the registry as berotralstat over placebo. In general, a ratio compares the estimated event rate in one group with the estimated rate in another. The record presents the primary comparisons as percentage reductions, with 95% confidence intervals and p-values. The 110 mg comparison is reported as a 30.0% reduction, and the 150 mg comparison as a 44.2% reduction. These are model-based relative comparisons, not raw differences between the displayed group rates.

A confidence interval gives a range of values compatible with the data and the statistical model under its assumptions. Its width reflects precision: a broad interval indicates more uncertainty about the magnitude of the comparison than a narrow interval. A p-value describes how inconsistent the observed data are with a specified null hypothesis, under the model assumptions. Neither measure gives the probability that the null hypothesis is true, and neither alone conveys clinical importance.

How should the re-calculations be read?

Re-calculations for continuous secondary outcomes use posted group summaries to produce simple, unadjusted comparisons. In general, this approach can provide a rough check on direction and scale, but it does not reproduce a model that adjusts for baseline values, repeated measurements, or other design features. The re-calculated confidence intervals and p-values may therefore differ from the sponsor’s analyses even when they use the same outcome data.

The continuous-outcome re-calculations estimate mean differences using group summaries. For some outcomes, the standard deviation used in the re-calculation is approximated from the reported standard errors. Such estimates should be treated as illustrative, not as a replacement for the registry’s reported analysis. The sponsor’s analysis takes precedence if a discrepancy is identified; the record does not flag a discrepancy for these results.

For count outcomes, a simple unadjusted comparison based on group means is not equivalent to the primary negative binomial regression. It does not incorporate the stated baseline-rate covariate or time-on-treatment offset in the same way. Consequently, the sponsor’s reported model-based primary comparison is the relevant result for interpreting the registered primary analysis.

What do the planning illustrations mean?

Planning illustrations use the observed effect as an assumed target and show participants per arm for 80% power and participants per arm for 90% power. They are not the trial’s observed power and do not show that the study was designed around those assumptions. The stated illustration assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation, with the effect to detect set to a stated fraction of the observed effect.

Observed effects can be unstable, especially when estimated from a small study. Planning for a smaller fraction of an observed effect yields a more conservative illustration than planning for the full observed effect. In general, power calculations also depend on assumptions about variability, allocation, outcome distributions, and the analysis method. The registry record does not report the trial’s own sample-size justification, so the illustrations should not be presented as evidence of the original design rationale.

10. Analyses Reported by the Sponsor

The registry reports the primary comparisons from a negative binomial regression model. For the 110 mg group versus placebo, the sponsor’s analysis reports a 30.0% reduction, a 95% confidence interval from 4.6% to 48.7%, and p = 0.024. For the 150 mg group versus placebo, it reports a 44.2% reduction, a 95% confidence interval from 23.0% to 59.5%, and p < 0.001. These are the posted analyses to use when describing the primary result.

Re-calculations based on summary statistics are simple, unadjusted checks. They do not recreate the negative binomial model, its baseline attack-rate covariate, or its offset for time on treatment. The primary result therefore should not be replaced by an estimate derived from the displayed group rates. The registry does not flag a discrepancy for the primary result, and no recalculated primary comparison is reported as a substitute.

For secondary continuous outcomes, the registry gives model-based analyses such as mixed-model repeated measures and ANCOVA. Their estimates and p-values can differ from simple unadjusted re-calculations because the methods and assumptions differ. Where both are discussed, the registry’s own analysis is the appropriate description of the sponsor-reported result; the re-calculation is only an illustrative check. It is not a competing analysis with equal standing.

11. Multiplicity, Missing Data and Analysis Populations

The registry describes two primary treatment comparisons: each of the berotralstat doses versus placebo. It reports a p-value and confidence interval for each. The record does not report whether or how the two primary comparisons were adjusted for multiplicity, or whether a hierarchy or other testing strategy was used. Without that information, the displayed p-values should be read as reported, not assumed to have a particular family-wise error interpretation.

The record also lists multiple secondary outcomes, including more than one comparison for some outcomes and outcomes across different periods. In general, when multiple hypotheses are tested, the chance of at least one apparently positive result by chance can rise. Adjustment methods or a prespecified testing sequence can help control this issue. The multiplicity plan for the secondary outcomes is not reported in the registry record, so individual secondary p-values warrant more caution than a single confirmatory test.

The primary population is explicitly defined as the intent-to-treat population, including all randomized subjects regardless of treatment administration. The record gives primary-outcome group counts, but the detailed handling of missing outcome data, incomplete follow-up, treatment discontinuation, and any imputation procedures is not reported in the registry record. The stated offset accounts for duration on treatment in the model, but that description alone does not explain how missing attack information was handled.

The registry record does not report whether interim analyses were planned or conducted, nor does it provide the sample-size justification. Those details should not be inferred from the posted outcome estimates or from planning illustrations based on observed effects. The available record supports describing the stated population, model, endpoint, and reported comparisons, but not reconstructing unreported statistical decisions.

12. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: diverticulum intestinal haemorrhagic (2.6%), pneumonia (2.6%), transient ischaemic attack (2.6%), plasma cell myeloma (1.8%), pleural effusion (1.8%).

The safety entries use denominators that differ from the primary-outcome group counts. For serious adverse events, the registry reports 5 events with 57 at risk in the 110 mg group, 5 with 58 at risk in the 150 mg group, and 2 with 39 at risk in the placebo group. For other adverse events, it reports 56 with 58 at risk, 53 with 57 at risk, and 30 with 39 at risk, respectively. Deaths are reported as 0 in each group.

These counts describe the registry’s safety reporting; they are not adjusted comparisons and do not by themselves establish whether an event was caused by treatment. The denominators differ between the serious-event and other-event entries and from the primary efficacy counts, so those populations should not be assumed to be identical. The registry also lists serious-event terms with percentages, including intestinal haemorrhagic diverticulum, pneumonia, and transient ischaemic attack. Those terms should be read as event listings, not as evidence of a causal relationship.

Safety interpretation depends on definitions, exposure time, event ascertainment, and follow-up, among other factors. Further details about these matters are not reported in the registry record. The posted figures are therefore best treated as descriptive safety data rather than as a stand-alone comparative safety analysis.

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

The registry’s primary analysis reports lower model-based HAE attack rates for each berotralstat dose compared with placebo during the 24-week treatment period. The reported comparisons are statistically distinguishable from no reduction under the stated analysis, with the 110 mg comparison reported at p = 0.024 and the 150 mg comparison at p < 0.001. The confidence intervals convey uncertainty about the size of each relative reduction.

These results do not establish that every participant benefited, or that an individual would have a particular attack rate. A group-level rate comparison describes average event frequency over the stated period. It does not reveal the full distribution of attacks among individuals, nor does it establish how results would differ outside the enrolled population or follow-up period.

The findings also do not establish that the 150 mg dose is superior to the 110 mg dose. The registry reports separate comparisons against placebo, not a direct active-dose comparison. A larger point estimate in one placebo comparison is not itself a statistical test of the difference between doses.

The primary result concerns investigator-confirmed attacks under a negative binomial model. It should not be conflated with quality of life, symptom days, expert-confirmed events, or longer-term outcomes. Those measures may add context but have their own definitions and analyses. The record does not report enough information to resolve every question about missing data, multiplicity, sample-size rationale, or interim analyses. The result is therefore evidence about the specified primary endpoint and comparisons, not a complete account of every possible benefit, harm, or longer-term outcome.

14. Why This Trial Matters Statistically

This trial illustrates why count outcomes need methods that reflect both event frequency and time under observation. The primary endpoint is not simply the number of attacks in each group: it is an attack rate per 28 days, and the stated model incorporates treatment duration through an offset. The analysis also includes baseline attack rate as a covariate. Readers can therefore distinguish the model-based treatment comparison from a direct subtraction of the displayed group estimates.

It also demonstrates the importance of identifying the estimand and analysis population. The registry defines the primary population as all randomized subjects regardless of treatment administration. That definition clarifies who is intended to contribute to the primary efficacy analysis, while the record’s limited reporting on missing outcomes leaves important implementation details unresolved.

Another statistical lesson is that two dose-versus-placebo results do not answer whether the doses differ from each other. That requires a direct comparison and its uncertainty. The trial’s posted primary analyses do not report one. Likewise, multiple secondary outcomes can support a broader descriptive picture, but without a reported multiplicity strategy, their individual p-values should be interpreted cautiously.

Finally, the registry’s model-based results and simple re-calculations have different roles. The sponsor’s negative binomial analysis addresses the registered primary endpoint using the stated covariates and offset. Summary-statistic re-calculations are useful only as transparent, unadjusted illustrations. Keeping those methods distinct helps prevent a convenient re-analysis from being mistaken for the trial’s primary inference.

15. Limitations

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

The registry record leaves several trial-specific statistical details unreported. It does not give the sample-size justification, so the enrollment cannot be evaluated against a documented design target from this record alone. Planning illustrations based on observed effects are not evidence of the trial’s original power assumptions or its observed power.

The record describes the negative binomial model components but does not report model diagnostics, the assessment of over-dispersion, or sensitivity analyses. It does not provide detailed missing-data procedures, including how incomplete attack reporting or treatment discontinuation was handled. The offset for duration on treatment is part of the stated model, but does not answer those questions by itself.

The registry does not report a multiplicity strategy for the primary dose comparisons or the numerous secondary outcomes. This limits interpretation of the set of p-values as a family of tests. It also does not report whether interim analyses occurred. These omissions do not negate the posted estimates, but they constrain what can be concluded about the overall testing plan.

The posted primary results are model-based and should be interpreted within the stated 24-week period and investigator-confirmed endpoint. The record does not report a direct comparison between doses. The difference in naming between BCX7353 in the trial title and berotralstat in the outcome and arm labels is not explained in the record. Finally, the safety denominators differ across entries; the registry does not provide enough detail in these figures alone to determine why, or to make an adjusted safety comparison.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: Efficacy and Safety Study of BCX7353 as an Oral Treatment for the Prevention of Attacks in HAE — NCT03485911.
• Registry record last updated 2023-06-26; status last verified 2023-05.
• Results first posted 2021-03-02.
• 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.

19. Record Summary

The registry describes a completed Phase 3 randomized, double-blind, placebo-controlled, parallel-group trial of oral BCX7353 for prevention of attacks in people with Type I or Type II hereditary angioedema. It lists triple masking and overall enrollment of 121. Primary efficacy analyses compare berotralstat 110 mg and 150 mg once daily separately with placebo.

The primary endpoint is the investigator-confirmed HAE attack rate per 28 days over the 24-week treatment period. The registry reports negative binomial model comparisons: a 30.0% reduction for the 110 mg dose and a 44.2% reduction for the 150 mg dose relative to placebo. Both comparisons are reported with 95% confidence intervals and p-values. The record also lists secondary outcomes and descriptive adverse-event data.

Important details, including the sample-size justification, multiplicity plan, missing-data handling, and interim-analysis information, are not reported in the registry record. The posted primary model results should be distinguished from unadjusted re-calculations and from broader conclusions that the record does not establish.