Efficacy and Safety of Odevixibat in Patients With Alagille Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Odevixibat in Patients With Alagille Syndrome (NCT04674761), a randomized phase 3 study. The primary outcome is Change From Baseline in Scratching Score.

2. Clinical Question

3. Trial Design

ASSERT was a Phase 3, randomized, placebo-controlled study of odevixibat in patients with Alagille syndrome. The registry record lists a parallel-group model and triple masking. The study is recorded as completed, with enrollment of 52. The record lists the start date as 2021-03-19 and primary completion as 2022-09-09.

Participants were assigned to odevixibat (A4250) or placebo. Both were oral capsules taken once daily for 24 weeks; the placebo capsules were intended to match the active treatment. The posted primary outcome is change from baseline in scratching score, assessed through Month 6, and the posted secondary outcome is change in serum bile acid levels. There are two posted outcome measures and two posted analyses, corresponding to the primary result and the secondary result.

The primary endpoint uses average morning and evening observed scratching scores. The baseline value was based on the 14 days before treatment began, while the endpoint describes the change for each four-week average through Month 6, with the final period specified as Weeks 21 to 24. The secondary measure compares baseline with the average of Week 20 and Week 24 serum bile acid values.

The registry record does not report the original sample-size justification, detailed eligibility criteria, randomization procedure, or the full protocol analysis plan. The posted group counts and estimates describe the reported outcomes; they do not establish what assumptions were used to design the trial.

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.

Overall Study

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 Change From Baseline in Scratching Score, measured over Change from baseline for each four-week average pruritis score to Month 6 (Weeks 21 to 24), in which baseline was calculated based on the 14 days before the start of treatment..

The primary endpoint is change from baseline in average observed scratching score. The Albireo Observer-Reported Outcome instrument assessed scratching twice daily: in the morning after waking and in the evening before bedtime. Each observation used a scale from 0, meaning no scratching, to 4, meaning worst possible scratching. The endpoint is the average AM and PM score, summarized through Month 6. Baseline was calculated from the 14 days before treatment began, and the final four-week average corresponds to Weeks 21 to 24.

This endpoint is used to represent observed scratching over time, rather than relying on a single observation. The scale’s direction matters: lower scores indicate less observed scratching, so a negative change from baseline indicates a decline in the recorded score. The comparison of interest is the difference in average change between the odevixibat and placebo groups. That contrast accounts for change in both groups and is more informative about their relative pattern than describing one group’s change alone.

The registry record does not report a threshold for what would count as a clinically important score change. Statistical evidence about a group difference therefore should not be treated as a direct measure of how meaningful the change would be to patients. The endpoint is also specifically an observer-reported score; it is not a direct measure of every aspect of symptoms or health.

7. Results Posted in the Registry

• Odevixibat (A4250): mean -1.69 versus -0.80 on control; difference -0.89 (95% CI -1.46 to -0.32), standardized effect d = -0.88; z-test p = 0.002.

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.

Serum Bile Acid Levels

• 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 errors.
• Result:
  • Odevixibat (A4250): mean -90.35 versus 22.39 on control; difference -112.74 (95% CI -182.46 to -43.02), standardized effect d = -0.91; z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Odevixibat (A4250) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry record posts one secondary outcome, serum bile acid levels. Its estimated change is negative in the odevixibat group and positive in the placebo group, so the direction of the group contrast is consistent with a larger reduction in the odevixibat group. The sponsor’s analysis reports a confidence interval that does not include zero. This provides additional statistical context alongside the primary scratching-score result, but it measures a different outcome on a different scale.

The secondary result should not be treated as equivalent to the primary result. The primary endpoint was designated as change in scratching score, while serum bile acid levels were secondary. A secondary outcome can help describe a broader pattern, but it does not replace the primary comparison or establish the same kind of evidence for the primary question.

The registry record does not report an adjustment for testing multiple outcomes. When several outcomes are examined, the chance of at least one apparently unusual result can increase if each is assessed without an adjustment. Therefore, an unadjusted secondary p-value carries less confirmatory weight than a result interpreted under a prespecified multiplicity strategy. The registry record does not report such a strategy, so the secondary result is best regarded as supportive and exploratory in its statistical status, without assuming a particular analysis plan.

The posted outcome list contains only this secondary endpoint. The record does not describe whether other outcomes were measured but not posted, nor does it report how missing secondary measurements were handled. These reporting gaps limit assessment of the full outcome-testing context. The overall direction across the posted primary and secondary results can be noted, while keeping their distinct roles and levels of evidential weight clear.

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

• Serum Bile Acid Levels

9. Statistical Interpretation

10. Statistical Methods Explained

What does a least-squares mean represent?

A least-squares mean is a model-based estimate of a group’s average outcome. In a trial analysis, the model can account for specified features of the data and design. It is not necessarily identical to a simple arithmetic average. The registry record identifies the primary parameter as a least-squares mean and reports the group estimates and their standard errors. It describes the sponsor’s comparison method as mixed models analysis. The precise model terms, covariance assumptions, and any other adjustment details are not reported in the registry record.

The primary comparison is the least-squares mean difference between the odevixibat and placebo groups. The reported difference is negative, consistent with a larger reduction in the scratching score in the odevixibat group, because lower scores represent less observed scratching. The estimate describes the contrast between group averages; it does not say that every participant experienced a reduction or that the group estimates apply identically to each participant.

What does the confidence interval add?

A confidence interval describes the uncertainty around an estimated contrast under the analysis assumptions. The primary reported 95% confidence interval extends from -1.44 to -0.33. Its position below zero indicates that the interval’s values all favor a more negative change in the odevixibat group relative to placebo on this scoring scale. The interval also conveys that the exact size of the difference is uncertain. It is not a range containing a specified proportion of individual participant outcomes, and it does not establish that the true effect has a particular probability of lying inside the interval.

The sponsor-reported analysis gives p = 0.001. A p-value assesses how compatible the observed data are with a null hypothesis of no group difference under the statistical model and its assumptions. It is not the probability that the null hypothesis is true, nor does it measure clinical importance. The unadjusted recalculation has p = 0.002, but it uses a simpler comparison from posted summary statistics. The sponsor’s own model-based analysis is the primary reported analysis.

Why can the recalculation differ?

The recalculated estimate uses the posted group summaries and an approximate pooled standard deviation. It is labeled unadjusted because it does not reproduce the sponsor’s mixed models analysis. The recalculated primary difference is -0.89, whereas the sponsor reports -0.88. Their confidence intervals are also similar but not identical. Such small differences are expected when calculations use different statistical approaches, model structures, or rounding. The record does not provide the full model specification needed to recreate the sponsor’s analysis exactly.

The standard errors describe uncertainty in the estimated group means, not the spread of individual scores. The posted group summaries give standard errors of 0.174 for odevixibat and 0.233 for placebo. The recalculation’s pooled standard deviation is explicitly approximate. A standard deviation describes variation among observations; a standard error describes uncertainty in an estimated mean. These measures answer different questions and should not be interchanged.

How should the secondary analysis be understood?

The serum bile acid endpoint is also analyzed using a least-squares mean difference and a mixed models analysis. The endpoint is change from baseline to the average of Week 20 and Week 24 values. Its reported contrast is -112.74, with a 95% confidence interval from -178.78 to -46.69; the reported p-value is below 0.001. The registry record labels this analysis as superiority. These results are a separate endpoint analysis, not an additional primary outcome.

The posted recalculation for this endpoint is unadjusted and uses the summary data. As with the primary endpoint, it should be distinguished from the sponsor’s model-based result. The unadjusted analysis is useful as a transparent approximate comparison, but it is not a replacement for the reported analysis or its assumptions.

What does over-dispersion mean in general?

In general, over-dispersion means that observed variability is greater than a statistical model assumes. It can make standard errors too small if the model fails to account for the extra variation, which in turn can make confidence intervals too narrow and p-values too optimistic. This is a general statistical consideration, not a reported finding about ASSERT. The posted continuous outcomes and summary statistics do not establish that over-dispersion occurred, and the registry record does not report an assessment of it.

11. Confidence Intervals and Precision

The primary sponsor-reported estimate is a least-squares mean difference of -0.88, with a 95% confidence interval from -1.44 to -0.33. This interval indicates uncertainty about the magnitude of the group contrast while remaining on the negative side of zero. In the context of the scale, negative values correspond to a greater reduction in scratching score in the odevixibat group than in the placebo group. The interval is compatible with a range of differences, rather than specifying one exact effect.

The unadjusted recalculation gives a difference of -0.89 and a 95% confidence interval from -1.46 to -0.32. The estimates and intervals are close, but they are not identical. The sponsor’s analysis uses mixed models, while the recalculation is an unadjusted comparison based on posted summary statistics. The sponsor-reported estimate is the analysis to prioritize when describing the trial result.

A confidence interval is not a prediction interval for individual participants, and it does not indicate how many participants improved. It describes uncertainty in the estimated group contrast under the analysis assumptions. The standard errors reported alongside the group means provide information about uncertainty in those means, but they do not show the full distribution of individual scores.

The registry record does not report a threshold for clinical importance, so statistical precision cannot be translated into a judgment about whether the difference is meaningful in daily life. It also does not give model details or missing-data procedures needed to fully evaluate the assumptions behind the interval. The interval supports a statistical comparison, but precision and clinical interpretation remain distinct questions.

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

The 80% power column gives the illustrative number of participants per arm for a design intended to have an 80% chance of detecting the effect used in that scenario, if the assumptions hold. The 90% power column gives the corresponding per-arm planning figure for a design intended to have a 90% chance. These are planning targets for a hypothetical future study under the listed assumptions, not a measure of the probability that the observed trial result is correct.

The rows describe planning for 100%, 75%, and 50% of the observed effect. As the assumed effect becomes smaller, more participants per arm are needed to achieve the stated power targets. This occurs because smaller group differences are harder to distinguish from random variation. The figures are calculated from the observed effect and should not be read as the enrollment required by ASSERT or as evidence that the completed trial had a particular power. This is not observed power.

The same general interpretation applies to the sample-size illustrations associated with the secondary endpoint. Because these calculations use observed effects, they are sensitive to the estimated effect size and to the simplifying planning assumptions. The registry record does not report whether these assumptions match the original trial design.

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 = -0.890; pooled standard deviation σ = 1.008.
2. n = 2 × (1.96 + 0.842)² × 1.008² / -0.890² = 20.1, rounded up to 21 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 <- -0.89                      # observed difference in means
sigma <- 1.0079191237396                     # 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(4674761)
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 = 21 (80% power), 27 (90% power)
 75% of observed effect: n per arm = 36 (80% power), 48 (90% power)
 50% of observed effect: n per arm = 81 (80% power), 108 (90% power)
power.t.test: 21.1 
Simulated power at n = 21 per arm: 0.798 (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 own primary analysis is reported as a mixed models analysis. It estimates a least-squares mean difference of -0.88, with a 95% confidence interval from -1.44 to -0.33 and p = 0.001. The registry labels the analysis as superiority. These are the posted trial-analysis results and should take precedence over a recalculation from summary statistics.

The recalculated primary contrast is -0.89, with a 95% confidence interval from -1.46 to -0.32 and an unadjusted p-value of 0.002. This calculation is a simple unadjusted comparison based on the posted group summaries and approximate pooled variation. Its close agreement with the sponsor result is a useful consistency check, but it does not reproduce the mixed models analysis. The differences between the estimates, intervals, and p-values reflect that the calculations are not identical and may also reflect rounding.

The registry record does not report the detailed model specification or the information necessary to reconstruct the sponsor analysis. The comparison should therefore be understood as a comparison between the reported model-based result and an approximate summary-statistic recalculation, not as a test of which method is correct.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a multiplicity-adjustment procedure. It identifies a primary scratching-score endpoint and a secondary serum bile acid endpoint, but it does not state whether the statistical plan controlled the overall type I error across these analyses or how any hierarchy among outcomes was handled. Without that information, the primary and secondary p-values should not be interpreted as if a multiplicity strategy were documented. The secondary result in particular is unadjusted in the posted recalculation and should carry less confirmatory weight.

The record also does not report the handling of missing outcome data. It does not specify whether participants with incomplete assessments were excluded, whether imputation was used, or how the mixed models analysis addressed missing measurements. These details matter because the analysis can be affected by the amount and pattern of missing data and by the assumptions used to handle it. No particular missing-data mechanism or method can be inferred from the posted results.

The analysis population is not reported in the registry record. The group counts in the outcome summaries are 35 for odevixibat and 17 for placebo, but the record does not explain whether the primary analysis used all randomized participants, a modified intention-to-treat population, or another defined population. It also does not report how adherence or protocol deviations were addressed in the analysis.

Randomization and masking are reported, but key analysis details remain unavailable. The record does not report the full statistical analysis plan, model terms, prespecified subgroup analyses, or interim analysis procedures. These omissions do not negate the posted estimates, but they constrain an independent assessment of how analyses were selected and how robust the results are to analytic choices.

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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pyrexia (5.9%), cerumen impaction (5.9%), otitis media chronic (5.9%), subcutaneous abscess (5.9%), adenoidal hypertrophy (5.9%).

The registry record reports serious adverse events among 5 participants in the odevixibat group and 2 in the placebo group. The numbers at risk for these summaries are 35 and 17, respectively. It reports 26 participants with other adverse events in the odevixibat group and 12 in the placebo group. Deaths are recorded as 0 in both groups.

These are group-level safety counts. They do not describe the severity, duration, timing, relatedness to treatment, or outcome of every event. The record lists several serious-event terms, including pyrexia, cerumen impaction, chronic otitis media, subcutaneous abscess, adenoidal hypertrophy, and increased international normalised ratio. The listed percentages are registry-reported event percentages; they should be interpreted in the context of the event definitions and reporting procedures, which are not detailed in the posted record.

Counts should not be treated as a complete comparison of safety without further information about exposure, follow-up, event ascertainment, and whether individuals experienced more than one event. Those details are not reported in the registry record. These summaries describe reported events and do not establish causation.

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

The primary result describes a difference in average change in observed scratching score between the randomized groups. The sponsor-reported estimate is negative, and the confidence interval is entirely below zero. On the scale used, that pattern indicates a greater reduction in the recorded score in the odevixibat group than in the placebo group during the reported assessment period. The statistical result is evidence about the group contrast under the reported analysis and its assumptions.

It does not mean that every participant’s score changed in the same way. Group averages can coexist with substantial variation in individual outcomes, and the posted summary does not show each participant’s response. The registry record also does not report a threshold for a clinically important difference, so the statistical estimate alone cannot establish how meaningful the contrast is to patients or caregivers.

The result does not establish that the observed difference is free from bias or uncertainty. Interpretation depends on the analysis population, missing-data handling, model assumptions, and prespecified analysis choices; several of these are not reported in the registry record. The unadjusted recalculation is close to the sponsor estimate, but it does not independently validate all assumptions of the sponsor’s model.

The serum bile acid outcome gives a separate secondary result, not a replacement for the primary endpoint. Because multiplicity handling is not reported, it has less confirmatory weight. Safety counts describe reported adverse events but do not establish whether an event was caused by treatment or provide a complete account of comparative safety.

Overall, the posted data support a statistical difference in the primary group comparison as analyzed. They do not by themselves answer questions about individual benefit, clinical importance, longer-term outcomes, or effects beyond the participants and assessment period represented in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why the choice and definition of an endpoint matter in clinical research. The primary outcome is not simply a symptom label; it is an observer-reported score measured in the morning and evening, on a defined scale, over a specified treatment period. The direction of that scale determines how to read negative changes and group differences. Clear interpretation depends on linking the sign of the estimate to what higher and lower scores mean.

It also demonstrates the distinction between a group’s change from baseline and the comparison between groups. Both groups show negative average changes, but the statistical question is whether their changes differ. The between-group estimate and its confidence interval address that question more directly than either group mean on its own.

ASSERT also provides a useful example of model-based trial reporting alongside a summary-statistic recalculation. The sponsor’s mixed models result and the approximate unadjusted recalculation are close, yet they are not interchangeable. Model details and analysis populations help readers understand what each estimate represents; those details are not reported in the registry record.

Finally, the record distinguishes a primary outcome from a secondary outcome and reports safety counts separately. That organization matters because several outcomes do not automatically have equal evidential status. Without a reported multiplicity strategy, secondary statistical findings require more cautious interpretation. A clear registry record supports careful reading not only of estimates and p-values, but also of what remains undocumented.

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 the posted record for this trial. The primary endpoint is an observer-reported scratching score, with morning and evening assessments averaged over time. The record does not report a threshold for clinical importance, so the statistical contrast cannot be translated into a stated level of meaningful change. The score also represents observed scratching, not every aspect of symptoms or functioning.

The sponsor’s analysis is described as mixed models analysis, but the model specification is not reported. The registry record does not provide the full statistical analysis plan, the analysis population, or the approach to missing measurements. It is therefore not possible from the posted information to determine how those choices may influence the estimate or to reproduce the sponsor analysis precisely.

The record does not report a multiplicity strategy despite posting a primary and a secondary outcome. The secondary result should consequently be interpreted with caution rather than treated as a confirmatory finding on the same footing as the primary endpoint. The original sample-size justification and design assumptions are also not reported; the displayed planning illustrations based on observed effects do not fill that gap.

The safety summaries give counts but do not provide detailed information about exposure time, event timing, treatment relatedness, recurrent events, or the full circumstances of each event. The listed serious-event terms do not by themselves establish cause. These limits concern the completeness of the registry reporting and should be kept distinct from the numerical results that are posted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Odevixibat in Patients With Alagille Syndrome — NCT04674761.
• Registry record last updated 2023-11-02; status last verified 2023-10.
• Results first posted 2023-11-02.
• 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.

23. Record Summary

NCT04674761, titled “Efficacy and Safety of Odevixibat in Patients With Alagille Syndrome,” is the completed Phase 3 ASSERT study. The registry describes a randomized, triple-masked, parallel-group, placebo-controlled design and enrollment of 52. Odevixibat and matching placebo were administered as oral capsules once daily for 24 weeks.

The primary endpoint was change from baseline in average observed scratching score through Month 6. The sponsor-reported mixed models analysis estimated a least-squares mean difference of -0.88, with a 95% confidence interval from -1.44 to -0.33 and p = 0.001. The posted secondary outcome was change in serum bile acid levels. The record also reports adverse-event counts and deaths.

The registry record does not report the original sample-size justification, analysis population, missing-data procedures, multiplicity strategy, or full model specification. Those gaps limit assessment of the posted results beyond the reported estimates and their stated uncertainty.