A Study of Pegasys (Peginterferon Alfa-2a) Versus Untreated Control in Children With HBeAg Positive Chronic Hepatitis B: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Pegasys (Peginterferon Alfa-2a) Versus Untreated Control in Children With HBeAg Positive Chronic Hepatitis B (NCT01519960), a randomized phase 3 study. The primary outcome is Percentage of Participants With HBeAg Seroconversion at 24 Weeks After End of Treatment (EOT)/POP in Groups A and B.

2. Clinical Question

The registry describes a Phase IIIb, parallel-group study of peginterferon alfa-2a versus untreated control. The key statistical contrast is between Group A, receiving treatment without advanced fibrosis, and Group B, the untreated control without advanced fibrosis. Group C, for children with advanced fibrosis, does not form part of that randomized comparison. The switch group is also distinct: it consists of control participants who could later receive treatment under the study’s switch arrangement.

These design features define the scope of the primary comparison. The results do not directly estimate a randomized treatment contrast in children with advanced fibrosis, nor do they compare treatment with control after participants in the switch group have changed treatment status. The registry record does not report a separate primary comparison for those groups.

3. Trial Design

The study is recorded as randomized, open label, parallel group, and Phase IIIb. Enrollment was 165. The registry reports a start date of 2012-07-11, primary completion on 2015-07-09, and a completed status. These are record-level details; the listed enrollment does not mean that every enrolled participant contributed to every endpoint or analysis.

Children without advanced fibrosis and without cirrhosis were randomized 2:1 to Group A, peginterferon alfa-2a, or Group B, untreated control. Treatment was planned for 48 weeks. Children with advanced fibrosis were assigned to Group C and received treatment; they were not part of the randomized A-versus-B comparison. The registry also describes a switch arrangement under which control participants who had not experienced seroconversion 48 weeks after randomization could enter a treatment period. That offer was available for 1 year following 48 weeks from randomization.

The primary endpoint was assessed at follow-up 24 weeks after the end of treatment or the principal observation period, with the timeframe described as up to 72 weeks overall. The brief summary states that participants were followed for 5 years after the relevant treatment or observation period. Long-term follow-up groups are listed separately in the safety information, so their observations should not be conflated with the primary randomized endpoint.

Open-label status means participants and study personnel were not masked to assignment, as indicated by the registry. The record does not report further details about procedures to limit assessment bias, the randomization sequence, allocation concealment, stratification factors, adherence, or handling of treatment changes in the primary analysis. It also does not report the original sample-size justification or the complete protocol-level statistical plan. Those details should not be inferred from the posted results.

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: A total of 211 individuals were screened for entry into the study. Of these, there were 161 participants enrolled in the study and included in the main analyses.

Overall Study

Reasons for not completing this period:

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 Percentage of Participants With HBeAg Seroconversion at 24 Weeks After End of Treatment (EOT)/POP in Groups A and B, measured over FU Week 24 (up to 72 weeks overall).

The primary endpoint is the percentage of participants with HBeAg seroconversion at follow-up 24 weeks after the end of treatment or principal observation period. The registry defines seroconversion as loss of hepatitis B e antigen (HBeAg) and the presence of hepatitis B e antibody (anti-HBe). It is therefore a combined laboratory outcome: loss of HBeAg alone is not sufficient under the stated definition.

This type of endpoint expresses how many participants in each group met a specified outcome, rather than measuring the time until an event. The percentage gives a group-level description of the observed outcome frequency. The accompanying 95% confidence interval communicates uncertainty around that estimated percentage, particularly relevant when outcome counts are limited.

HBeAg seroconversion was selected as the primary measure in this trial’s registry record. In general, a clearly defined primary endpoint helps focus interpretation on a prespecified main question and reduces the temptation to select whichever result appears most favorable among many outcomes. The registry record does not explain the scientific rationale for choosing this endpoint over other measures, so that rationale is not reported in the registry record.

The primary analysis is described as intention-to-treat, including all randomized participants regardless of treatment received. This definition preserves the comparison by randomized assignment as stated in the record, although the registry does not give further details about missing endpoint observations or the exact procedures used to retain participants with incomplete follow-up.

7. Results Posted in the Registry

• Group A: PEG-IFN Monotherapy Without Advanced Fibrosis: 25.7% (26/101) versus 6.0% (3/50) on control; risk difference 19.7 percentage points (95% CI 9.0 to 30.5), risk ratio 4.29 (1.36–13.50); unadjusted two-proportion z-test p = 0.004.

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.

Percentage of Participants With Loss of HBeAg at 24 Weeks After EOT/POP in Groups A and B

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Group A: PEG-IFN Monotherapy Without Advanced Fibrosis: 25.7% (26/101) versus 6.0% (3/50) on control; risk difference 19.7 percentage points (95% CI 9.0 to 30.5), risk ratio 4.29 (1.36–13.50); unadjusted two-proportion z-test p = 0.004.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Group A: PEG-IFN Monotherapy Without Advanced Fibrosis than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Hepatitis B Surface Antigen (HBsAg) Seroconversion at 24 Weeks After EOT/POP in Groups A and B

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Group A: PEG-IFN Monotherapy Without Advanced Fibrosis: 7.9% (8/101) versus 0.0% (0/50) on control; risk difference 7.9 percentage points (95% CI 2.7 to 13.2); unadjusted two-proportion z-test p = 0.041.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Group A: PEG-IFN Monotherapy Without Advanced Fibrosis than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Normal ALT at 24 Weeks After EOT/POP in Groups A and B

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Group A: PEG-IFN Monotherapy Without Advanced Fibrosis: 51.5% (52/101) versus 12.0% (6/50) on control; risk difference 39.5 percentage points (95% CI 26.2 to 52.8), risk ratio 4.29 (1.98–9.30); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Group A: PEG-IFN Monotherapy Without Advanced Fibrosis than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover several related laboratory and clinical measures assessed at follow-up, including HBeAg loss, HBsAg seroconversion, ALT normalization, viral-DNA thresholds, and combinations of seroconversion with viral-DNA criteria. The subset with results displayed includes measures that broadly point in the same direction as the primary comparison. These outcomes are related to the primary endpoint but are not interchangeable: each uses a different definition and captures a different aspect of the participants’ follow-up status.

The primary endpoint is specifically defined as HBeAg loss together with the presence of anti-HBe. A secondary measure of HBeAg loss alone does not require the antibody component, while measures involving HBsAg, ALT, or viral DNA address other features. Similar direction across some measures can add context, but it does not prove that the measures represent the same biological outcome or that one can stand in for another. The record does not report results for every one of the listed secondary measures in the registry record for this analysis.

Unadjusted secondary comparisons carry less weight than a prespecified primary analysis when many outcomes are examined. In general, testing many outcomes increases the chance that at least one result appears statistically notable by chance. Unless a multiplicity strategy is specified and applied, nominal p-values for secondary outcomes should be treated as exploratory rather than as independent confirmation. The registry record does not report a multiplicity adjustment or a hierarchy governing interpretation of the secondary outcomes.

The secondary findings therefore provide supporting context, not a separate basis for a definitive claim. Their interpretation depends on each outcome’s definition, completeness of follow-up, and the analysis method. The broader set of outcomes also makes it important to distinguish a consistent pattern from confirmatory evidence established under a reported statistical plan.

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

• Percentage of Participants With Loss of HBeAg at 24 Weeks After EOT/POP in Groups A and B
• Percentage of Participants With Hepatitis B Surface Antigen (HBsAg) Seroconversion at 24 Weeks After EOT/POP in Groups A and B
• Percentage of Participants With Normal ALT at 24 Weeks After EOT/POP in Groups A and B
• Percentage of Participants With HBV Deoxyribonucleic Acid (DNA) <20,000 International Units Per Milliliter (IU/mL) at 24 Weeks After EOT/POP in Groups A and B
• Percentage of Participants With HBV DNA <2,000 IU/mL at 24 Weeks After EOT/POP in Groups A and B
• Percentage of Participants With Combined HBeAg Seroconversion and HBV DNA <20,000 IU/mL at 24 Weeks After EOT/POP in Groups A and B
• Percentage of Participants With Combined HBeAg Seroconversion and HBV DNA <2,000 IU/mL at 24 Weeks After EOT/POP in Groups A and B
• Percentage of Participants With HBeAg Seroconversion at EOT/POP in Groups A and B

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary for each participant: the registry definition is either met or not met at the specified follow-up assessment. A binary endpoint can be summarized as a count and a percentage in each group. The registry reports percentages and 95% confidence intervals, and defines the analysis population as all randomized participants regardless of treatment received.

What does a confidence interval express?

In general, a confidence interval describes the uncertainty associated with an estimated quantity under the statistical method used. A narrower interval indicates greater precision; a wider interval indicates less precision. It does not mean that a particular percentage of individual participants fall within the interval, and it does not remove potential bias in how participants were selected, treated, followed, or assessed. For this endpoint, the intervals around the two group percentages show that the observed percentages are estimates rather than exact underlying rates.

What does the odds ratio measure?

The sponsor’s reported analysis uses a Cochran-Mantel-Haenszel method and presents an odds ratio. In general, odds compare the frequency of an event with the frequency of no event; an odds ratio compares those odds across groups. It is a relative measure, so its numerical size is not the same as an absolute percentage-point difference. When the event is not rare, an odds ratio can appear more pronounced than a risk ratio, and it should not be translated directly into a probability for an individual.

The Cochran-Mantel-Haenszel method is generally used to estimate an association while accounting for strata. The registry does not report the strata used or give enough detail to reconstruct the sponsor’s analysis. The reported odds ratio and its interval should therefore be understood as the registry’s sponsor analysis, not as a fully auditable calculation from the brief outcome summaries alone. The record also reports a Breslow-Day test with p = 0.373. In general, that test assesses whether odds ratios differ across strata; its presence does not by itself establish which strata were used or validate all assumptions of the main analysis.

Why is there also a recalculation?

A simple recalculation from posted group summary statistics can give readers an unadjusted comparison on an absolute scale. The risk difference is the difference between the event proportions in the groups. Here, the recalculated estimate is 0.197, with a 95% confidence interval from 0.090 to 0.305. The recalculated unadjusted p-value is 0.004. These calculations do not reproduce the sponsor’s stratified analysis, and the record flags a discrepancy. For that reason, the sponsor’s own analysis takes precedence; the unadjusted calculation is supplementary and should not be treated as the definitive inferential result.

How should the p-value be read?

In general, a p-value evaluates how compatible the observed data are with a specified null hypothesis under the statistical model and assumptions used. It is not the probability that the null hypothesis is true, nor a measure of clinical importance. The registry reports p = 0.004 for the sponsor’s primary analysis and the recalculation reports an unadjusted p-value of 0.004. Those values relate to different analytical approaches and should not be presented as though they were the same test. Neither value accounts automatically for the many outcomes recorded in the trial.

Why does over-dispersion matter?

For a binary endpoint, the variation in the observed count is usually modeled through the event probability and the number of observations. In general, over-dispersion means the data vary more than the assumed model allows. If present and unaccounted for, it can make standard errors too small and confidence intervals too narrow. The registry record does not report an over-dispersion assessment or describe a model requiring such an adjustment. It should not be assumed either that over-dispersion occurred or that it was tested and ruled out.

The stated confidence intervals for the group percentages were calculated using the Pearson-Clopper method. In general, this is an exact binomial interval method for a proportion. It can be useful when event counts are modest, but an interval for each group percentage answers a different question from an interval for the between-group contrast. The reported odds-ratio interval and the recalculated risk-difference interval concern comparisons between groups; they should not be confused with the separate group-level intervals.

The registry’s intention-to-treat description says participants were analyzed regardless of treatment received. That preserves randomized assignment as the basis for group membership, in principle. However, the registry does not report the number with missing primary endpoint observations, the assumptions used for missing data, or any imputation or sensitivity analyses. An analysis-population label alone cannot show how incomplete follow-up affected the result.

11. Confidence Intervals and Precision

The group-level 95% confidence interval for Group A is 17.56 to 35.4, and the interval for Group B is 1.25 to 16.55. These intervals indicate uncertainty around the respective observed percentages. They are not confidence intervals for the difference between groups. The comparative uncertainty is instead represented by the sponsor’s odds-ratio interval, 1.54 to 19.2, and by the recalculated unadjusted risk-difference interval, 0.090 to 0.305.

The sponsor’s odds-ratio interval spans a wide range of relative effects. This means that although the reported point estimate is 5.43, the data are compatible with a substantially smaller or larger odds ratio under the reported method. The interval does not include the null value for an odds ratio, but that observation is not a substitute for considering the analysis method, multiplicity, missing data, and the scope of the randomized population. The recalculated risk-difference interval also has a meaningful width, showing uncertainty about the size of the absolute contrast.

In general, confidence-interval precision depends on the amount of information in the data and the method used. The registry gives 101 participants in Group A and 50 in Group B for the primary endpoint display. Those group sizes, together with the observed event counts and the chosen methods, contribute to uncertainty. No new precision estimate should be inferred for the advanced-fibrosis or switch groups from the primary comparison.

The registry’s group percentage intervals use the Pearson-Clopper method, whereas the sponsor’s comparative analysis is described as Cochran-Mantel-Haenszel. Different statistical quantities and methods naturally produce different interval widths and interpretations. The discrepancy flag also counsels against treating the recalculation as an exact reproduction of the sponsor’s result. Overall, the posted results support a direction of difference in the randomized groups, while the magnitude remains less precisely estimated than the point estimates alone might suggest.

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 estimates are illustrations based on the observed effect, not the original design calculation for this trial. For this binary endpoint, the estimates are participants per arm, not total events. They use the stated assumptions of a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The registry record does not report the trial’s own original sample-size assumptions or justification.

The 80% power column describes the number of participants per arm in the illustration that would give an 80% chance of detecting the specified effect under the listed assumptions, if that effect and the model assumptions were correct. The 90% power column describes the corresponding planning number for a 90% chance. These are design calculations, not guarantees about the result of a future study and not measures of the probability that the observed result is true.

The rows use planning for 100% of the observed effect, planning for 75% of the observed effect, and planning for 50% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants under otherwise identical assumptions. The estimates should therefore be read as scenarios tied to a particular assumed effect size, rather than as a recommendation or a reconstruction of the actual trial plan.

This is not observed power. Observed power calculated from the same result adds little beyond the estimate and its uncertainty; it should not be used to decide whether the finding is real. The illustration also assumes equal allocation, whereas the randomized treatment and control allocation in the trial was described as 2:1. It is consequently a generic planning comparison, not a direct forecast of this study’s allocation or 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.060; treatment proportion p₁ = 0.257; average p̄ = 0.159.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5168 = 1.0128.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4976 = 0.4188.
4. n = (1.0128 + 0.4188)² / (0.1974)² = 52.6, rounded up to 53 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
p0 <- 0.06                          # control proportion
p1 <- 0.257425742574257                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1519960)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 53 (80% power), 70 (90% power)
 75% of observed effect: n per arm = 82 (80% power), 110 (90% power)
 50% of observed effect: n per arm = 156 (80% power), 208 (90% power)
power.prop.test: 52.6 
Simulated power at n = 53 per arm: 0.827 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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’s sponsor analysis reports a Cochran-Mantel-Haenszel odds ratio of 5.43, with a 95% confidence interval from 1.54 to 19.2 and p = 0.004. It also reports a Breslow-Day test with p = 0.373. The available record does not give enough detail to reconstruct the strata or all steps of the sponsor’s analysis from the outcome summaries.

The accompanying recalculation uses the posted summary statistics to produce a simple unadjusted risk difference of 0.197, with a 95% confidence interval from 0.090 to 0.305, and an unadjusted p-value of 0.004. It is a different estimand and method from the sponsor’s odds-ratio analysis. The recalculated odds ratio and confidence interval also differ slightly from the sponsor’s reported values.

The record flags this discrepancy. Accordingly, the sponsor’s own analysis takes precedence for describing the trial’s reported inferential result. The recalculation can help readers see the unadjusted contrast on an absolute scale, but it does not correct, replace, or independently verify the sponsor’s stratified analysis. The registry does not report an explanation for the difference, so its cause is not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists many outcome measures, including a primary endpoint and numerous secondary outcomes. Testing several outcomes creates a multiplicity issue: in general, the more comparisons examined, the greater the chance that some may appear noteworthy even if there is no underlying difference for those outcomes. A prespecified hierarchy, family-wise error control, false-discovery control, or another stated strategy can clarify how to interpret a set of tests.

A multiplicity procedure or plan is not reported in the registry record. It is therefore not possible to determine whether the sponsor adjusted the secondary analyses, reserved formal inference for a subset, or treated those analyses as exploratory. The primary p-value should not be assumed to account for all outcomes simply because it is the primary endpoint. Unadjusted secondary results warrant more cautious interpretation than a result tied to a clearly stated primary testing strategy.

The record identifies the primary population as intention-to-treat: all randomized participants regardless of treatment received. This is useful because it identifies randomized assignment as the intended basis for analysis. However, the record does not report how missing primary endpoint values were handled, how many values were missing, whether participants with incomplete follow-up were included in particular denominators, or whether sensitivity analyses were conducted. Those details matter because missing outcomes can affect both the estimated percentages and uncertainty.

The registry also does not report the full statistical analysis plan, interim-analysis procedures, stopping rules, or original sample-size rationale. These omissions do not establish that such procedures were absent; they mean the details are not reported in the registry record. Likewise, the listed Breslow-Day result does not reveal all features of the sponsor’s stratified analysis. Interpretation should remain bounded by the analyses and definitions that are explicitly recorded.

Finally, the randomized inference applies to the groups without advanced fibrosis or cirrhosis. Assignment of children with advanced fibrosis to treatment and the later switch opportunity change treatment exposure outside the main randomized comparison. Results from those groups cannot be treated as randomized comparisons against untreated control without a separately reported analysis and appropriate assumptions.

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: nephropathy (3.0%), pneumonia (3.0%), suicidal ideation (2.0%), alanine aminotransferase increased (1.0%), aspartate aminotransferase increased (1.0%).

The safety record lists serious adverse events for the main groups and for the advanced-fibrosis, switch, and long-term follow-up groups. In the primary treatment group, 6 participants were recorded as affected by a serious adverse event among 101 at risk; in the untreated-control group, 1 was affected among 49 at risk. The registry lists zero deaths in each of the displayed safety groups. These figures describe the recorded safety summaries and should not be read as a causal comparison on their own.

The registry’s top serious-event terms include nephropathy at 3.0%, pneumonia at 3.0%, suicidal ideation at 2.0%, alanine aminotransferase increased at 1.0%, aspartate aminotransferase increased at 1.0%, and osteochondrosis at 1.0%. The record does not give enough detail in these summaries to assess event timing, duration, severity beyond the serious-event classification, relatedness to treatment, or the denominator used for each listed term. These percentages are not a complete account of all adverse events.

Group C and the switch group had different treatment and selection pathways from the randomized comparison. Long-term follow-up is also listed separately. Their safety counts should therefore be read within their own group and follow-up context, not pooled into a randomized treatment-versus-control contrast.

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

The posted primary results describe the proportion of participants in the randomized groups without advanced fibrosis or cirrhosis who met the registry definition of HBeAg seroconversion at the specified follow-up. The observed percentage was higher in Group A than in Group B, and the sponsor’s reported odds-ratio analysis gives a statistically notable comparison under its stated method. The confidence intervals show that the estimated group percentages and comparative effect are not known with complete precision.

This result does not show that every participant in the treatment group experienced seroconversion, or that no participant in the untreated group did. It does not establish an individual participant’s outcome, and a group-level odds ratio is not an individual probability. Nor does the endpoint alone establish the broader clinical consequences, durability beyond the specified assessment, or long-term status of each participant.

The result applies to the randomized comparison described in the record. It does not supply a randomized treatment contrast for children with advanced fibrosis, who were assigned to treatment, or for control participants who later entered the switch group. The primary analysis is described as intention-to-treat, but missing-data procedures are not reported in the registry record. Open-label conduct and the absence of further methodological detail also limit what can be concluded about potential assessment or analysis biases.

The recalculated unadjusted risk difference offers an absolute-scale description, but the record flags a discrepancy with the sponsor’s analysis. The sponsor’s own analysis takes precedence. Secondary outcomes provide additional context, yet their multiplicity and the absence of a reported adjustment plan mean they should not be treated as equivalent independent confirmation. The careful conclusion is about the posted endpoint and comparison, not a general claim beyond the population, outcome definition, and follow-up recorded.

18. Why This Trial Matters Statistically

This trial illustrates why the definition of an endpoint matters. HBeAg seroconversion is not simply loss of HBeAg in the registry’s definition; it also requires the presence of anti-HBe. A statistical comparison is only interpretable when the event being counted is clear and the assessment time is specified. The primary outcome is tied to follow-up 24 weeks after the end of treatment or principal observation period, rather than to an unspecified point during treatment.

It also shows why absolute and relative measures should be distinguished. The sponsor reported an odds ratio, while a simple unadjusted recalculation gives a risk difference. Both are ways of describing a contrast, but they answer on different scales and are not interchangeable. Confidence intervals add information about the uncertainty in those estimates, which a point estimate or p-value alone cannot convey.

The design makes the target comparison important. Randomization applies to the groups without advanced fibrosis or cirrhosis, while the advanced-fibrosis group was assigned treatment and the switch arrangement changes exposure for some control participants. A single trial record can therefore contain groups whose results answer different questions. Treating all groups as if they were randomized in the same way would misstate the evidence.

Finally, the record presents a primary analysis alongside many secondary outcomes, but does not report a multiplicity plan or detailed missing-data procedures. This is a useful reminder that statistical significance, precision, endpoint selection, and analysis transparency all contribute to interpretation. The stated findings are most informative when kept within those boundaries.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The main comparison is limited to children without advanced fibrosis or cirrhosis. Children with advanced fibrosis were assigned to treatment rather than randomized to untreated control, so their outcomes cannot provide the same randomized contrast. Participants who entered the switch group also had a different treatment pathway from those who remained untreated, limiting direct comparison after switching.

The study was open label. The registry record does not report whether outcome assessment was blinded or what procedures were used to limit possible assessment bias. The primary endpoint is based on laboratory markers, but the available record does not describe assay methods, central laboratory procedures, or handling of values near any laboratory thresholds.

The primary endpoint display gives 101 participants in Group A and 50 in Group B, while the safety summary lists 49 at risk for Group B. The registry does not explain the difference in these analysis counts. The missing-data handling, endpoint-specific denominators, and sensitivity analyses are not reported in the registry record. The intention-to-treat description does not by itself resolve those questions.

The record contains a discrepancy between the sponsor’s reported analysis and the simple unadjusted recalculation. The sponsor’s own analysis takes precedence, but the reason for the discrepancy is not reported. Details needed to reproduce the sponsor’s stratified analysis, including the strata and fuller analysis plan, are also not reported in the registry record.

Many secondary outcomes are listed, and no multiplicity strategy is reported. The trial’s original sample-size assumptions, interim analyses, and complete statistical plan are not reported. These omissions constrain assessment of the planned inferential framework; they should not be interpreted as proof that particular procedures were or were not used. Follow-up duration also differs across the treatment, observation, switch, and long-term follow-up descriptions, so results must be interpreted at the timepoint specified for each outcome.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Pegasys (Peginterferon Alfa-2a) Versus Untreated Control in Children With HBeAg Positive Chronic Hepatitis B — NCT01519960.
• Registry record last updated 2022-11-18; status last verified 2022-10.
• Results first posted 2016-08-17.
• 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

NCT01519960 is a completed Phase IIIb, randomized, open-label, parallel-group study of peginterferon alfa-2a versus untreated control in children with HBeAg-positive chronic hepatitis B. The principal randomized comparison was between children without advanced fibrosis or cirrhosis assigned to treatment or untreated control. Children with advanced fibrosis were assigned to treatment, and a switch option was described for some control participants.

The primary endpoint was HBeAg seroconversion at follow-up 24 weeks after the end of treatment or principal observation period, defined as loss of HBeAg with anti-HBe present. The sponsor reported a Cochran-Mantel-Haenszel odds ratio of 5.43, with a 95% confidence interval from 1.54 to 19.2 and p = 0.004. A discrepancy is flagged between that analysis and the unadjusted recalculation, so the sponsor’s analysis takes precedence.

The registry record does not report the original sample-size justification, multiplicity plan, or detailed missing-data procedures. Secondary outcomes and safety summaries add context but do not replace the primary randomized comparison or remove these interpretive limits.