Trial Evaluating Efficacy and Safety of Dasiglucagon in Children With Congenital Hyperinsulinism: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Trial Evaluating Efficacy and Safety of Dasiglucagon in Children With Congenital Hyperinsulinism (NCT04172441), a randomized phase 2, phase 3 study. The primary outcome is Mean Intravenous Glucose Infusion Rate.

2. Clinical Question

3. Trial Design

This was a randomized trial with a double-blind, placebo-controlled crossover component in Part 1 and an open-label component in Part 2. The registry lists the trial as Phase 2 and Phase 3, with quadruple masking and a crossover model. It reports 12 participants enrolled and a completed status.

In Part 1, participants followed one of two treatment sequences. One sequence received dasiglucagon for 48 hours and then placebo for 48 hours; the other received placebo first and then dasiglucagon for 48 hours. The dasiglucagon infusion in Part 1 started at 10 µg/hour. Part 2 followed with 21 days of dasiglucagon infusion. The crossover lets each participant contribute observations during both Part 1 treatment periods, while randomization determines the order of treatments.

The registry describes the primary endpoint as the mean intravenous glucose infusion rate in the last 12 hours of each Part 1 treatment period, specifically Hours 36-48 after initiation of the trial drug. This timing focuses the primary comparison on the end of each 48-hour period. Part 2 was open-label, so its treatment and results should be understood separately from the blinded placebo comparison in Part 1.

The registry lists congenital hyperinsulinism as the condition and Zealand Pharma as the sponsor. It records the trial start as 2020-06-19 and primary completion as 2022-02-17. Details of the trial's original sample-size justification, planned interim analyses, and full statistical analysis plan are not reported in the registry 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.

Part 1-1: First Intervention (48 Hours)

Part 1-2: Second Intervention (48 Hours)

Part 2: Open Label Dasiglucagon

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 Mean Intravenous Glucose Infusion Rate, measured over Hours 36-48 after initiation of trial drug (Part 1).

The primary endpoint is the mean intravenous glucose infusion rate, measured in mg/kg/minute. It represents the average rate at which intravenous glucose was administered during the last 12 hours of each Part 1 treatment period, Hours 36-48 after treatment initiation. The registry reports this endpoint as a mean with standard deviation.

The endpoint was used because the trial objective concerned glucose requirements among children who needed continuous intravenous glucose to prevent or manage hypoglycemia. A lower mean infusion rate during a treatment period would indicate that less intravenous glucose was being administered during that measurement window. This describes the measured outcome; it does not by itself establish why the rate changed or what the change means for an individual child.

In a crossover trial, the same participant can contribute a measurement under each treatment, allowing comparison within participants as well as across treatment sequences. The registry's reported primary analysis used a mixed models analysis and reported a difference in least-squares means. The model specification, including its treatment of period and sequence effects, is not reported in the registry record.

The endpoint is a measure of glucose infusion, not a direct measurement of every aspect of hypoglycemia or overall clinical status. Other registered outcomes include carbohydrate administration, time to weaning off intravenous glucose, hypoglycemia events, hospital discharge, and pancreatic surgery. Those outcomes address related but distinct questions.

7. Results Posted in the Registry

• Dasiglucagon: mean 4.33 versus 9.51 on control; difference -5.18 (95% CI -9.42 to -0.94), standardized effect d = -0.98; z-test p = 0.017.

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.

Carbohydrates Administered

• 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:
  • Dasiglucagon: mean 106.70 versus 139.10 on control; difference -32.40 (95% CI -76.86 to 12.06), standardized effect d = -0.58; z-test p = 0.153.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dasiglucagon and the control. The interval gives the range of effects that remain compatible with the data.

Mean Intravenous Glucose Infusion Rate

• 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:
  • Dasiglucagon: mean 6.90 versus 10.40 on control; difference -3.50 (95% CI -8.00 to 1.00), standardized effect d = -0.62; z-test p = 0.127.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dasiglucagon and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists 21 secondary outcomes, spanning glucose and carbohydrate administration, hypoglycemia events, and time-to-event measures such as weaning from intravenous glucose, hospital discharge, and pancreatic surgery. The detailed continuous secondary results include carbohydrate administration and a 48-hour mean intravenous glucose infusion rate. Together, these measures address related aspects of glucose support but are not identical to the primary endpoint's final 12-hour measurement window.

Across the detailed secondary results, the evidence is not uniformly aligned in statistical strength. The registry includes a model-based analysis for carbohydrate administration, while the posted 48-hour infusion-rate comparison has no model-based analysis listed. That variation means the secondary outcomes offer contextual evidence rather than a single consistent confirmation of the primary analysis. They also cover different time windows and quantities, so a difference in one measure need not imply the same pattern in another.

General statistical context: when many outcomes are examined, some may appear statistically notable by chance even when there is no underlying effect for those outcomes. Unless the analysis accounts for multiplicity, the usual p-values do not control the overall chance of a false-positive finding across the full set of tests. The registry record does not report a multiplicity adjustment for secondary outcomes. Accordingly, unadjusted secondary findings carry less weight than the primary comparison and should be treated as exploratory context rather than as independent proof.

Secondary endpoints may still help describe whether the primary result sits within a broader pattern of measured outcomes. Their usefulness depends on transparent analysis methods, complete outcome reporting, and consideration of the number of comparisons. The registry record does not provide enough information to assess all those features across every listed secondary measure.

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

• Carbohydrates Administered
• Mean Intravenous Glucose Infusion Rate
• Mean Intravenous Glucose Infusion Rate Below 10 mg/kg/Minute
• Time to Complete Weaning Off Intravenous Glucose
• Hypoglycemia Event Rate in Part 2
• Clinically Significant Hypoglycemia Events in Part 2
• Time to Actual Hospital Discharge
• Time to Pancreatic Surgery

9. Statistical Interpretation

10. Statistical Methods Explained

General statistical context: a mean summarizes the central level of a continuous measurement, while a standard deviation describes how dispersed individual measurements are around that mean. The registry reports standard deviations for the treatment-period infusion rates. Standard deviations describe variation among measurements; they are not confidence intervals for the treatment effect.

What does the treatment difference represent?

The primary treatment comparison is expressed as a difference in least-squares means. A least-squares mean is a model-based estimate of a group or treatment-period mean, adjusted according to the model's included terms. The registry reports the modeled difference as -5.21 mg/kg/minute for dasiglucagon relative to placebo. A negative value means the modeled mean in the dasiglucagon period was lower than the modeled mean in the placebo period, given that comparison's direction.

The registry identifies the method as a mixed models analysis. In general, mixed models can account for correlations among repeated measurements from the same participant and can include terms describing the design. That is relevant to a crossover trial, where participants contribute measurements under both treatments. The registry record does not report the model formula, the covariance structure, or which design terms were included. Those details should not be inferred from the method label alone.

Why distinguish the model result from recalculation?

The recalculated estimate is a simple, unadjusted comparison based on the posted treatment-period means and standard deviations. It yields a mean difference of -5.18 mg/kg/minute and p = 0.017. This is a useful check on the broad direction and scale of the result, but it is not a reconstruction of the sponsor's mixed model. In particular, a summary-statistic recalculation does not use the participant-level crossover structure or any model adjustments that may have been used in the registry analysis.

The registry's own analysis reports a difference in least-squares means of -5.21 mg/kg/minute, a 95% confidence interval from -8.29 to -2.13, and p = 0.004. These are the sponsor-reported model results. The recalculation and sponsor analysis answer related questions but use different statistical approaches. The registry does not flag a discrepancy between them.

What does a p-value say?

General statistical context: a p-value measures how compatible the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, nor does it quantify the size or clinical importance of an effect. A p-value also does not express the chance that the result will replicate. Interpretation depends on the design, analysis choices, and precision of the estimate.

The registry reports p = 0.004 for its primary mixed models analysis. The recalculation reports p = 0.017. These values arise from different analyses and should not be treated as interchangeable. The registry's method and estimated treatment difference are the central record-based results; the unadjusted recalculation is supplementary.

Why does crossover structure matter?

General statistical context: crossover designs compare treatments within the same participants. This can account for stable differences between participants, but observations from one person are correlated rather than independent. The sequence and timing of treatment periods can also matter. A suitable analysis generally needs to reflect the repeated-measures structure and the design's period or sequence features. The registry reports a mixed models analysis but does not report enough model detail to evaluate those choices independently.

The treatment sequences were randomized, and Part 1 was described as double-blind and placebo-controlled. Part 2 was open-label and consisted of dasiglucagon infusion. Because Part 2 did not include a placebo period, it does not supply a concurrent placebo comparison equivalent to the primary Part 1 contrast.

What do the uncertainty measures add?

General statistical context: a confidence interval gives a range of effect values compatible with the data and the statistical model at the stated confidence level. It communicates uncertainty about the estimated effect, whereas a p-value summarizes evidence against a null value under the model. A confidence interval should be read together with the estimate and with the design limitations. Its width is influenced by the amount and variability of data and by the analysis.

The sponsor-reported 95% confidence interval for the primary difference extends from -8.29 to -2.13 mg/kg/minute. The whole interval is below zero, so the reported model's compatible values point in the same direction as the point estimate. The interval nevertheless spans a range of possible effect magnitudes; the point estimate is not known without uncertainty. The registry's original planning assumptions and full analysis plan are not reported, so the reported analysis cannot be compared against an undocumented protocol specification.

11. Confidence Intervals and Precision

The registry's mixed models analysis estimates a primary difference in least-squares means of -5.21 mg/kg/minute. Its 95% confidence interval runs from -8.29 to -2.13 mg/kg/minute. Because the entire interval is below zero, the model-based estimate is consistent with a lower mean infusion rate during the dasiglucagon period than during the placebo period. The endpoints of the interval also show that the estimate is not exact: the data are compatible with a range of negative differences under the reported model.

General statistical context: a confidence interval reflects sampling uncertainty under the assumptions of the analysis. It is not a range that contains every participant's response, and it does not show the full distribution of individual outcomes. Nor does a 95% confidence interval mean that there is a 95% probability that this particular interval contains the fixed true effect. The interpretation depends on repeated use of the method under its assumptions.

The primary endpoint had 12 observations in each treatment period, within a crossover trial of 12 enrolled participants. This is limited information for estimating both an average treatment difference and its variability. The interval is consequently important alongside the point estimate; readers should not treat the point estimate as a precise value that applies identically to all participants.

The unadjusted recalculation also gives a negative mean difference, -5.18 mg/kg/minute, but its uncertainty calculation differs from the mixed model. The registry's model-based confidence interval is the relevant interval for interpreting the sponsor-reported analysis. The registry record does not provide enough detail to independently evaluate the model's assumptions or reproduce its interval from participant-level data.

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 table and curve are planning illustrations based on the observed effect, not the trial's original design calculations. The registry's own sample-size assumptions are not reported. The illustration assumes a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It considers an effect equal to the observed effect and smaller effects set at 75% or 50% of the observed effect.

The figures are participants per arm, not total participants, for the continuous outcomes in this illustration. The assumptions describe a two-arm comparison, while the actual primary design was a crossover; the illustration should therefore be read as a simplified planning reference rather than a reconstruction of the trial design. The registry's general sample-size note says time-to-event tables give total events, but that convention does not apply to these continuous-outcome figures.

The 80% power column gives the illustrative number of participants per arm for an 80% chance of detecting the selected effect under the stated assumptions, if that effect and assumptions were correct. The 90% power column gives the corresponding planning number for a 90% chance. For example, planning for 75% of the observed primary effect gives 30 participants per arm for 80% power and 40 participants per arm for 90% power. Planning for 50% of the observed effect gives 66 participants per arm for 80% power and 89 participants per arm for 90% power.

Smaller effects are harder to distinguish from random variation, so the illustration requires more participants for smaller effects. These are planning numbers, not observed power, and they do not establish what power the completed trial had.

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 = -5.180; pooled standard deviation σ = 5.301.
2. n = 2 × (1.96 + 0.842)² × 5.301² / -5.180² = 16.4, rounded up to 17 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 <- -5.18                      # observed difference in means
sigma <- 5.30118425448503                     # 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(4172441)
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 = 17 (80% power), 23 (90% power)
 75% of observed effect: n per arm = 30 (80% power), 40 (90% power)
 50% of observed effect: n per arm = 66 (80% power), 89 (90% power)
power.t.test: 17.5 
Simulated power at n = 17 per arm: 0.784 (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 registry reports a mixed models analysis for the primary endpoint. It gives a difference in least-squares means of -5.21 mg/kg/minute, a 95% confidence interval from -8.29 to -2.13, and p = 0.004. This is the sponsor's reported analysis and reflects the model-based comparison entered in the record.

The simple recalculation from the posted summary statistics gives a mean difference of -5.18 mg/kg/minute and p = 0.017. It is unadjusted and does not reproduce the reported mixed model. The fact that the estimates point in the same direction does not make the methods equivalent: the sponsor's analysis is model-based, while the recalculation uses only summary statistics.

The registry does not flag a discrepancy between the calculations. The recalculation is best treated as a supplementary check, not as a replacement for the reported analysis. The record does not include enough detail about the model specification or participant-level data to reproduce the sponsor's result independently.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and lists 21 secondary outcomes. It reports a mixed models analysis for the primary comparison and gives selected secondary analyses, but a multiplicity strategy is not reported in the registry record. It is therefore not possible to determine from the record whether the analysis plan used a hierarchy of hypotheses, an adjustment across outcomes, or another approach to control the overall false-positive risk.

General statistical context: testing several outcomes increases the opportunity for apparently unusual results to arise by chance. A multiplicity procedure can adjust how evidence is evaluated across related tests. Without a stated procedure, secondary p-values should not be interpreted as if each were the only test conducted. This limitation is especially relevant when the secondary outcomes cover multiple measures and time points.

The registry record also does not report how missing measurements were handled, whether any participants were excluded from particular analyses, or the precise analysis populations. The enrollment count and endpoint sample counts are reported, but they do not establish whether all randomized participants contributed to every analysis or how unavailable measurements were treated. The handling of missing data can affect estimates and uncertainty, especially when missingness is related to outcomes or treatment.

The primary endpoint is measured during two Part 1 treatment periods in a crossover design. The registry reports a mixed models method but does not give its specification, its assumptions about missing observations, or details of period and sequence terms. Those details are needed to assess the analysis fully. The record also does not report an interim-analysis plan or the trial's original sample-size justification. These omissions limit independent assessment of the analysis plan; they do not by themselves show that the reported analysis was inappropriate.

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: acute respiratory failure (8.3%), respiratory distress (8.3%).

The serious adverse event figures are reported separately by treatment period and follow-up grouping. In Part 1, the registry records zero participants with serious adverse events among 12 at risk during dasiglucagon and zero among 12 at risk during placebo. In Part 2, it records one participant with a serious adverse event among 12 at risk. The combined Parts 1 and 2 grouping also records one among 12, and the follow-up grouping records zero among one participant at risk. No deaths are listed in these groups.

The registry lists acute respiratory failure and respiratory distress as serious adverse event terms, each reported as 8.3%. These terms should be read as the record's listed events, not as an estimate of comparative risk. The figures come from a small trial and include different treatment periods and groupings; the Part 1 placebo-controlled comparison should not be conflated with the open-label Part 2 period.

Serious adverse event counts are not the same as all adverse events. The registry also reports participants with other adverse events, but those are a separate category. These figures describe events recorded in the trial and do not, on their own, establish that treatment caused an event or determine the overall safety profile.

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

The primary result is a comparison of mean intravenous glucose infusion rates during the final 12 hours of dasiglucagon and placebo periods in Part 1. The registry's mixed models analysis estimates a lower mean rate during the dasiglucagon period, with a 95% confidence interval that remains below zero. The unadjusted recalculation points in the same direction, but the registry's model-based analysis is the reported primary result.

This finding applies to the trial's measured endpoint, its Part 1 time window, and the children enrolled in this trial who required continuous intravenous glucose. It does not establish what would happen for every child with congenital hyperinsulinism, nor does a group mean describe the response of each participant. The registry reports 12 participants enrolled, so the evidence comes from a small study.

The result does not establish that every secondary outcome changed in the same way. Secondary measures address different quantities and time periods, and the record does not report a multiplicity strategy. Nor does the Part 1 placebo comparison establish an effect for Part 2, which was open-label and did not include a placebo treatment period.

General statistical context: statistical evidence, effect magnitude, precision, and clinical importance are distinct considerations. A confidence interval describes uncertainty under the analysis; it does not determine whether an effect is important to patients or whether it changes care. The registry does not report a threshold for a clinically meaningful difference in infusion rate. No clinical recommendation follows from these statistical results alone.

18. Why This Trial Matters Statistically

This trial presents a crossover comparison in a small pediatric population for whom intravenous glucose requirements are central to the study objective. Statistically, the design matters because each participant received both dasiglucagon and placebo during Part 1. The treatment periods are therefore linked within individuals, and a suitable analysis needs to reflect that structure rather than treating the periods as unrelated groups.

The primary result illustrates why the reported model and a simple recalculation should be distinguished. Both give a negative estimate, but the registry's mixed models analysis is the result intended to represent the trial's modeled comparison. The summary-statistic recalculation offers a check on direction and scale, while lacking the full crossover information and model specification.

The confidence interval adds information beyond whether a p-value is considered notable: it displays a range of effect magnitudes compatible with the reported model. The small enrollment and the absence of a reported original sample-size justification also make it important to avoid treating the point estimate as definitive. Planning illustrations based on the observed effect are not a substitute for the trial's own design rationale.

Finally, the registry includes multiple secondary outcomes and safety groupings. Their statistical interpretation depends on transparent reporting of analysis populations, missing-data handling, and multiplicity methods. Those details are not reported in the registry record. This trial is therefore a useful example of how design, analysis, precision, and reporting completeness all shape interpretation of a clinical result.

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.

The trial enrolled 12 participants, limiting the amount of information available for estimating treatment effects and describing variability. Although the crossover design allows within-participant comparison in Part 1, the registry record does not provide participant-level data or sufficient model details to independently verify how within-person correlation, period effects, or sequence effects were handled.

The primary outcome is a mean infusion rate measured during a specified 12-hour window at the end of each treatment period. It does not capture every aspect of glucose management or hypoglycemia, and the registry does not report a threshold for a clinically meaningful change in this measure. The Part 2 period was open-label and lacked a placebo comparison, so it cannot provide the same blinded contrast as Part 1.

The record does not report the original sample-size justification, the full statistical analysis plan, handling of missing data, exact analysis populations, or multiplicity procedures. It also does not report enough model specification to reproduce the sponsor's mixed models analysis. These missing details restrict independent assessment of potential analytic choices and of the robustness of secondary findings.

There are many registered secondary outcomes, but their posted analyses are not described in equal detail. Unadjusted findings across multiple outcomes may be less reliable as confirmatory evidence. The serious adverse event data also come from few participants and are divided across treatment periods and follow-up groupings, so the counts offer limited information for comparing uncommon events.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Trial Evaluating Efficacy and Safety of Dasiglucagon in Children With Congenital Hyperinsulinism — NCT04172441.
• Registry record last updated 2025-03-14; status last verified 2025-03.
• Results first posted 2025-03-14.
• 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

The registry record describes a completed randomized Phase 2 and Phase 3 trial of dasiglucagon in children with congenital hyperinsulinism. Part 1 was a double-blind, placebo-controlled crossover comparison; Part 2 was open-label and involved 21 days of dasiglucagon infusion. The record reports 12 participants enrolled.

The primary endpoint was mean intravenous glucose infusion rate during the last 12 hours of each Part 1 treatment period. The sponsor-reported mixed models analysis estimated a difference in least-squares means of -5.21 mg/kg/minute, with a 95% confidence interval from -8.29 to -2.13. A simple unadjusted recalculation gives -5.18 mg/kg/minute and p = 0.017, but does not reproduce the crossover model.

The registry lists 21 secondary outcomes and reports serious adverse event information by period and follow-up grouping. Important details—including the original sample-size justification, missing-data handling, analysis populations, multiplicity strategy, and full model specification—are not reported in the registry record.