A Study of PEGASYS (Peginterferon Alfa-2a (40KD)) in Patients With Hepatitis Be Antigen (HBeAg) Positive Chronic Hepatitis B (CHB).: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of PEGASYS (Peginterferon Alfa-2a (40KD)) in Patients With Hepatitis Be Antigen (HBeAg) Positive Chronic Hepatitis B (CHB). (NCT00435825), a randomized phase 4 study. The primary outcome is Percentage of Participants With Hepatitis Be Antigen (HBeAg) Seroconversion 24 Weeks Following End of Treatment.

2. Clinical Question

The outcome required both a negative HBeAg result and a positive anti-HBe result. The trial therefore examined a defined laboratory response after treatment, rather than a general measure of health or a comparison with no treatment. The registry record lists 551 participants enrolled and describes random assignment to the four regimens. Its brief summary states that every group had a treatment-free follow-up period for assessment of the primary endpoint.

The posted results report primary outcome percentages of 14.08% for 90 μg over 24 weeks, 22.86% for 180 μg over 24 weeks, 25.76% for 90 μg over 48 weeks, and 36.15% for 180 μg over 48 weeks. These are descriptive results for the registry-defined per-protocol population. They do not, by themselves, establish that one regimen is preferable or explain how the results may apply beyond the participants and analysis population in this trial.

3. Trial Design

This was a phase 4, randomized, double-blind, parallel-group study sponsored by Hoffmann-La Roche. It enrolled 551 participants with chronic hepatitis B and compared four active treatment regimens. The record gives the study start as 2007-03 and primary completion as 2010-12; its current status is completed.

The four arms combined two weekly doses with two treatment durations: 90 μg or 180 μg of peginterferon alfa-2a for 24 weeks or 48 weeks. Each regimen was administered subcutaneously once a week. The brief summary describes a 24-week treatment-free follow-up after treatment in all groups. It gives the primary outcome assessment as 24 weeks after treatment ended, which corresponds to Week 48 for the 24-week regimens and Week 72 for the 48-week regimens.

Randomization and double blinding are stated in the registry record. The record does not report the method used to generate the allocation sequence, how allocation was concealed, or how blinding was maintained. It does not identify a placebo arm; the posted comparisons use the 90 μg for 24 weeks regimen as the reference and compare the other active groups against it.

The brief summary states a target sample size of 500+ individuals. The rationale or formal calculation behind that target is not reported in the registry record. The original trial’s planned effect size, power, significance threshold, allocation assumptions, and any adjustment for multiple comparisons are also not reported. Planning illustrations based on observed results are separate from the trial’s original design assumptions.

For the primary endpoint, the registry record defines the population as participants who received study drug and had no major protocol deviation. It also says participants were analyzed according to treatment received rather than randomized treatment. The description notes that 10 participants in the per-protocol population switched treatment groups, but the remainder of that sentence and further details about those switches 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per-protocol population defined as all participants who received study drug and who did not have any major protocol deviation. Patients were analyzed according to the treatment received, rather than the randomized treatment. 10 patients in the per-protocol population switched treatment groups for the analysis.

5. Baseline Characteristics

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

Population: Baseline Measures are based on participants from the Intent-to-treat population who received study drug.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Hepatitis Be Antigen (HBeAg) Seroconversion 24 Weeks Following End of Treatment, measured over 24 Weeks following end of treatment (Week 48 for 24 Week Treatment or Week 72 for 48 Week Treatment).

The primary endpoint was the percentage of participants with HBeAg seroconversion 24 weeks after the end of treatment. The registry definition requires both absence of HBeAg, indicated by a negative test result, and presence of anti-HBe, indicated by a positive test result. This is a binary outcome: each participant either met the stated laboratory definition at the specified assessment or did not.

The assessment time depended on assigned treatment duration. For participants treated for 24 weeks, the primary assessment was at Week 48; for participants treated for 48 weeks, it was at Week 72. In both cases, the intended timing was 24 weeks after treatment ended. This timing describes a response following a treatment-free interval, rather than an assessment while treatment was still being given.

For a binary endpoint, the percentage gives an understandable summary of how often the defined event occurred in each group. The registry also reports 95% confidence intervals around the group percentages. These intervals convey uncertainty in the estimated percentages; they do not establish that every participant’s outcome is known beyond the recorded assessment or resolve limitations in the analysis population.

As a general statistical point, a clearly defined laboratory endpoint can support consistent classification across participants when the measurement and timing are applied as specified. Its interpretation remains tied to that definition and follow-up time. It is not, by itself, a measure of every aspect of disease status, long-term outcomes, or safety.

7. Results Posted in the Registry

• Peginterferon Alfa-2a 180 μg_24 Weeks: 22.9% (32/140) versus 14.1% (20/142) on control; risk difference 8.8 percentage points (95% CI -0.2 to 17.8), risk ratio 1.62 (0.98–2.70); unadjusted two-proportion z-test p = 0.058.
• Peginterferon Alfa-2a 90 μg_48 Weeks: 25.8% (34/132) versus 14.1% (20/142) on control; risk difference 11.7 percentage points (95% CI 2.3 to 21.1), risk ratio 1.83 (1.11–3.01); unadjusted two-proportion z-test p = 0.015.
• Peginterferon Alfa-2a 180 μg_48 Weeks: 36.2% (47/130) versus 14.1% (20/142) on control; risk difference 22.1 percentage points (95% CI 12.0 to 32.1), risk ratio 2.57 (1.61–4.09); unadjusted two-proportion z-test p = <0.001.

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 Hepatitis Be Antigen (HBeAg) Seroconversion at Week 72

• 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:
  • Peginterferon Alfa-2a 180 μg_24 Weeks: 27.1% (38/140) versus 18.3% (26/142) on control; risk difference 8.8 percentage points (95% CI -0.9 to 18.6), risk ratio 1.48 (0.95–2.30); unadjusted two-proportion z-test p = 0.077.
  • Peginterferon Alfa-2a 90 μg_48 Weeks: 25.8% (34/132) versus 18.3% (26/142) on control; risk difference 7.4 percentage points (95% CI -2.4 to 17.3), risk ratio 1.41 (0.89–2.21); unadjusted two-proportion z-test p = 0.136.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Peginterferon Alfa-2a 180 μg_24 Weeks and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Peginterferon Alfa-2a 90 μg_48 Weeks and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Loss of Hepatitis Be Antigen (HBeAg) 24 Weeks Following End of Treatment

• 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:
  • Peginterferon Alfa-2a 180 μg_24 Weeks: 22.9% (32/140) versus 14.8% (21/142) on control; risk difference 8.1 percentage points (95% CI -1.0 to 17.1), risk ratio 1.55 (0.94–2.54); unadjusted two-proportion z-test p = 0.083.
  • Peginterferon Alfa-2a 90 μg_48 Weeks: 26.5% (35/132) versus 14.8% (21/142) on control; risk difference 11.7 percentage points (95% CI 2.2 to 21.3), risk ratio 1.79 (1.10–2.92); unadjusted two-proportion z-test p = 0.016.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Peginterferon Alfa-2a 180 μg_24 Weeks and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Peginterferon Alfa-2a 90 μg_48 Weeks than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Loss of Hepatitis B Surface Antigen (HBsAg) 24 Weeks Following End of Treatment

• 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:
  • Peginterferon Alfa-2a 180 μg_24 Weeks: 0.0% (0/140) versus 0.7% (1/142) on control; risk difference -0.7 percentage points (95% CI -2.1 to 0.7); unadjusted two-proportion z-test p = 0.320.
  • Peginterferon Alfa-2a 90 μg_48 Weeks: 2.3% (3/132) versus 0.7% (1/142) on control; risk difference 1.6 percentage points (95% CI -1.3 to 4.5), risk ratio 3.23 (0.34–30.64); unadjusted two-proportion z-test p = 0.279.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Peginterferon Alfa-2a 180 μg_24 Weeks and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Peginterferon Alfa-2a 90 μg_48 Weeks and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes span additional HBeAg measures, HBsAg outcomes, alanine aminotransferase normalization, HBV-DNA suppression thresholds, and a combined endpoint response. The posted results include a Week 72 HBeAg seroconversion measure and an HBeAg loss measure, as well as HBsAg loss. The record also lists other secondary outcomes, but detailed estimates for those remaining outcomes are not reported in the registry record.

At a broad level, the secondary HBeAg results follow a pattern that is compatible with the primary finding: the higher observed percentages generally occur in the longer-duration and/or higher-dose regimens. This broad agreement can be informative because the outcomes concern related aspects of hepatitis B antigen response. It does not make the secondary findings independent confirmation of the primary result; related outcomes can share participants, measurements, and underlying biological processes.

The HBsAg loss outcome is distinct from the primary HBeAg seroconversion definition. It is a separate laboratory endpoint and should not be treated as interchangeable with HBeAg response. The secondary outcomes also use different definitions and, in some cases, different thresholds or combinations of measures. Consequently, a consistent-looking pattern across outcomes does not establish that all outcomes tell the same clinical story.

Unadjusted secondary comparisons carry less weight because many outcomes and group contrasts can create opportunities for chance findings. The registry record does not report a multiplicity adjustment, a testing hierarchy, or a prespecified approach to interpreting the secondary analyses. The secondary findings are therefore best used as descriptive context and as a basis for questions to be examined in a planned analysis, rather than as separate definitive claims. Their confidence intervals and analysis-population limitations should be considered alongside those for the primary endpoint.

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

• Percentage of Participants With Hepatitis Be Antigen (HBeAg) Seroconversion at Week 72
• Percentage of Participants With Loss of Hepatitis Be Antigen (HBeAg) 24 Weeks Following End of Treatment
• Percentage of Participants With Hepatitis B Surface Antigen (HBsAg) Seroconversion 24 Weeks Following the End of Treatment
• Percentage of Participants With Loss of Hepatitis B Surface Antigen (HBsAg) 24 Weeks Following End of Treatment
• Percentage of Participants With Normal Alanine Aminotransferase (ALT)
• Percentage of Participants With Hepatitis B Virus Deoxyribonucleic Acid (HBV-DNA) Suppression < 20,000 IU/mL 24 Weeks Following End of Treatment
• Percentage of Participants With Hepatitis Deoxyribonucleic Acid (HBV-DNA) Suppression < 2,000 IU/mL 24 Weeks Following End of Treatment
• Percentage of Participants With Combined Endpoint Response 24 Weeks Following End of Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

What does a binary percentage describe?

The primary outcome is binary because it records whether each participant met the HBeAg seroconversion definition at the scheduled assessment. A group percentage summarizes the share meeting that definition. It is a useful descriptive measure, but it does not by itself quantify uncertainty or show whether a group differs from another. The registry reports a 95% confidence interval for each percentage to communicate uncertainty in the estimate.

How should the risk difference be read?

The pairwise comparisons use a risk difference, which contrasts the observed event proportions in two groups by subtraction. In these results, the reference is peginterferon alfa-2a 90 μg for 24 weeks. A positive estimate means the observed proportion was higher in the other regimen than in the reference group; a negative estimate would mean it was lower. The estimates and confidence limits are reported on the proportion scale, for example 0.088 with limits -0.002 and 0.178 for the 180 μg, 24-week comparison. They should not be confused with a relative risk or odds ratio.

As a general statistical point, a difference on the proportion scale is often straightforward to interpret because it compares absolute event proportions. Its uncertainty depends on the number of participants and events in both groups. Small event counts or limited group sizes can produce wide confidence intervals, making the plausible range of the difference broad.

What does a 95% confidence interval convey?

A confidence interval gives a range of estimates compatible with the observed data under the method used. In repeated use of the same procedure, 95% confidence intervals would cover the underlying parameter in 95% of such repetitions, as a general explanation. It is not a statement that there is a 95% probability that this particular interval contains the true value. For a risk difference, an interval spanning zero includes no difference among the values compatible with the data under that procedure. An interval wholly on one side of zero is less compatible with a zero difference under the same assumptions, but it does not address bias, multiplicity, or clinical importance.

What do the p-values add?

The posted pairwise p-values are unadjusted. A p-value describes how unusual a result at least as extreme as the observed one would be under a specified no-difference model and its assumptions. It is not the probability that the no-difference model is true, and it does not measure the size or importance of an effect. The value for 180 μg over 24 weeks is 0.058; for 90 μg over 48 weeks it is 0.015; and for 180 μg over 48 weeks it is < 0.001. The registry record does not report adjustments for the multiple comparisons or outcomes.

As a general point, when multiple tests are conducted, the chance of at least one apparently unusual result can increase if each test is judged separately. A prespecified testing hierarchy or multiplicity adjustment can address that issue, but either approach must be described to interpret adjusted claims. Such a plan is not reported in the registry record. The unadjusted results are therefore best treated as exploratory comparisons rather than as a complete confirmatory analysis.

What does randomization contribute, and what changes in this analysis?

Randomization is intended to balance known and unknown participant characteristics across groups on average. The study is described as randomized and double-blind, but the primary analysis population is per-protocol and is analyzed according to treatment received rather than randomized treatment. As a general statistical matter, excluding participants or moving them between groups after randomization may affect comparability, particularly if the reasons for doing so relate to prognosis or outcome. The record says 10 participants switched treatment groups and does not provide enough detail to assess the consequences. It does not report an intention-to-treat analysis.

The distinction matters because a treatment-policy question is usually addressed by retaining participants in their randomized groups, regardless of treatment received, while a per-protocol analysis focuses on a selected group meeting protocol conditions. The latter can describe outcomes among those meeting its criteria, but selection can weaken the protection from bias that randomization is meant to provide. This is a general interpretation of analysis populations, not a claim about the reasons for switching in this study.

What is not described in the analysis plan?

The registry record does not report the statistical analysis plan, a primary sample-size justification, missing-data methods, interim analyses, covariate adjustment, or a method for handling multiple comparisons. It reports no sponsor analyses in the posted analyses field. The posted risk differences and p-values are unadjusted calculations based on the group summaries, so they should not be mistaken for adjusted sponsor analyses. No discrepancy between a sponsor analysis and these calculations is flagged in the record.

As a general principle, a complete report would clarify how participants with missing endpoint measurements were handled, whether analysis choices were prespecified, and how inference was controlled across outcomes and comparisons. Without those details, interpretation must stay close to the reported percentages, confidence intervals, and unadjusted contrasts rather than implying a more comprehensive analysis than the registry describes.

11. Confidence Intervals and Precision

The primary group percentages are estimates, not exact population values. The 95% confidence intervals communicate their uncertainty. For 90 μg over 24 weeks, the reported percentage is 14.08% with an interval from 8.82% to 20.91%. For 180 μg over 24 weeks, it is 22.86% with an interval from 16.19% to 30.71%. For 90 μg over 48 weeks, it is 25.76% with an interval from 18.54% to 34.09%. For 180 μg over 48 weeks, it is 36.15% with an interval from 27.91% to 45.04%.

These ranges show that the precise percentage in the population remains uncertain. The intervals are not equally narrow, and estimates should not be read as if the displayed point values were exact. The group sizes in the primary outcome summaries range from 130.0 to 142.0, so the outcome estimates are based on a limited number of participants in each arm.

For direct comparison with 90 μg over 24 weeks, the risk-difference interval for 180 μg over 24 weeks runs from -0.002 to 0.178 and includes zero. The interval for 90 μg over 48 weeks runs from 0.023 to 0.211, while that for 180 μg over 48 weeks runs from 0.120 to 0.321. These intervals indicate different levels of precision and compatibility with a zero difference under the unadjusted comparison method. They do not account for possible bias from the per-protocol, treatment-received analysis or for multiple testing.

As a general statistical explanation, wider intervals indicate less precision, while narrower intervals indicate that the estimate is more tightly constrained by the data and method. A confidence interval does not capture every source of uncertainty: measurement, selection into the analysis population, missing outcomes, and analysis choices can matter as well. The registry record does not report enough detail to evaluate all of those sources.

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 illustrations describe planning scenarios based on observed effects; they are not the trial’s original sample-size calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario asks how many participants per arm would be needed to detect the stated fraction of the observed effect. The effect scenarios are 100%, 75%, and 50% of the observed effect. The original design assumptions and justification are not reported in the registry record.

The 80% power column represents a planning target that, under the stated assumptions and if the specified effect were real, would give the test an 80% chance of detecting it using the stated approach. The 90% power column uses a higher chance-of-detection target under those same assumptions. These are prospective planning quantities; they do not tell us the probability that the trial’s findings are correct.

The figures are participants per arm, not totals across both groups. The sample-size assumptions state that time-to-event examples, if present, would instead give total events; the comparisons discussed for this binary outcome are participant counts per arm. The rows for smaller fractions of the observed effect require more participants because smaller differences are harder to distinguish from sampling variation. Thus, the 50% scenario calls for larger group sizes than the 75% or 100% scenarios for the same comparison.

These figures are illustrations tied to effects observed in this trial, and those observed estimates are uncertain. They should not be treated as a retrospective verdict on whether the completed trial was adequately designed. This is not observed power.

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 = 0.141; treatment proportion p₁ = 0.229; average p̄ = 0.185.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5488 = 1.0756.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5453 = 0.4589.
4. n = (1.0756 + 0.4589)² / (0.0877)² = 306.0, rounded up to 306 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 <- 0.140845070422535                          # control proportion
p1 <- 0.228571428571429                          # 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(435825)
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 = 306 (80% power), 410 (90% power)
 75% of observed effect: n per arm = 520 (80% power), 695 (90% power)
 50% of observed effect: n per arm = 1,111 (80% power), 1,487 (90% power)
power.prop.test: 306 
Simulated power at n = 306 per arm: 0.802 (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. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a multiplicity strategy for the several active-regimen comparisons or the set of secondary outcomes. It also lists no reported analyses in the analyses field. The posted pairwise p-values are unadjusted, so they should be read as individual comparisons rather than as results from a documented family-wise testing procedure. Without a prespecified hierarchy or adjustment method, it is difficult to know which comparisons were intended to support formal confirmatory conclusions.

Missing-data methods are not reported in the registry record. The number of participants in the primary endpoint analysis groups is listed, but the record does not explain whether every enrolled participant had an endpoint result, how unavailable measurements were handled, or whether any imputation or sensitivity analysis was used. A missing-data method can influence binary outcome percentages if the availability of measurements is related to response.

The primary population is described as per-protocol, including participants who received study drug and had no major protocol deviation. The record says they were analyzed by treatment received rather than randomized treatment. It notes that 10 participants in this population switched treatment groups, but the available description is cut off and further information about the switches and their handling is not reported in the registry record. An intention-to-treat result is not reported.

As a general statistical point, an analysis that retains randomized assignments is often used to preserve the benefits of randomization, while per-protocol analyses can be affected by post-randomization selection. Neither approach removes all limitations, and transparent reporting of population definitions and missing-data handling is needed to judge the effect. The registry description does not provide enough detail to assess how these choices affected the posted results.

The original sample-size justification, assumptions about the target effect, and any interim-analysis plan are also not reported in the registry record. The planning illustrations based on observed effects are not a substitute for those original design details. These reporting gaps do not erase the descriptive percentages, but they limit how much can be concluded from the unadjusted inferential summaries.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: rib fracture (1.5%), extradural abscess (0.8%), clavicle fracture (0.8%), ligament injury (0.8%), drug hypersensitivity (0.8%).

The serious adverse event summaries list 4 affected participants among 144 at risk in the 90 μg, 24-week group; 4 among 141 in the 180 μg, 24-week group; 6 among 132 in the 90 μg, 48-week group; and 5 among 130 in the 180 μg, 48-week group. These are counts of participants with serious adverse events, not counts of all events, and they should be read with the corresponding at-risk group sizes.

The registry record lists serious event terms and percentages including rib fracture at 1.5%, and extradural abscess, clavicle fracture, ligament injury, drug hypersensitivity, and spinal cord compression at 0.8% each. The record does not provide enough information in these summaries to determine whether these terms occurred in more than one group or to compare their rates across regimens. Death counts are not reported in the registry record.

These descriptive figures do not establish whether a particular regimen caused an event or whether the groups differ in safety. The registry summaries do not report a comparative safety analysis, exposure-adjusted rates, or additional context needed to interpret individual events. They should be read as recorded event information, not as medical advice or a complete assessment of risk.

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

The posted results describe the proportion of participants meeting a specific laboratory definition of HBeAg seroconversion 24 weeks after treatment ended. Within the stated per-protocol analysis population, the observed percentage was highest in the 180 μg for 48 weeks group and lowest in the 90 μg for 24 weeks group. The direct unadjusted comparisons show uncertainty that varies by regimen: one risk-difference interval includes zero, while the intervals for the two 48-week comparisons do not.

Those results do not answer every question a reader may have about treatment. The endpoint is a laboratory response at a particular follow-up time; it is not itself a measure of symptoms, long-term clinical outcomes, or every aspect of hepatitis B status. The trial compared four active regimens and did not include a placebo or untreated group among the listed arms. It therefore provides comparisons between those regimens, not a direct comparison with no treatment.

The randomized, double-blind design is relevant to the trial’s intended comparison, but the primary results are reported for a per-protocol population and analyzed according to treatment received rather than randomized assignment. The record notes 10 treatment switches without reporting enough detail to assess their effect. Missing-data handling, the complete analysis plan, and multiplicity procedures are not reported, and the posted pairwise p-values are unadjusted.

Statistical evidence should be considered together with precision. The group estimates have 95% confidence intervals, and the direct comparisons also have intervals that show a range of plausible risk differences under the unadjusted method. A point estimate alone does not convey that uncertainty. Nor does a p-value state the probability that a regimen works or that an observed difference is real.

Accordingly, the registry record supports a descriptive account of observed responses across the active dose-and-duration groups, with some unadjusted comparisons favoring higher observed percentages in the compared group. It does not, on its own, establish a treatment recommendation, resolve safety questions, or determine how these results apply to people outside the analyzed trial population.

17. Why This Trial Matters Statistically

This trial is statistically informative because its four active arms vary both dose and duration. That structure allows readers to inspect outcomes across combinations rather than considering a single regimen in isolation. The observed primary percentages follow an ordered descriptive pattern across those combinations, while the pairwise estimates and confidence intervals show that the strength and precision of comparisons are not identical.

The study also illustrates why a group-level pattern is not a substitute for a prespecified analysis. Dose and duration change together across the four regimens, and each pairwise contrast uses one reference regimen. A pattern across arms can suggest questions about dose, duration, or their combination, but a formal claim about those components would depend on a stated analysis plan and appropriate contrasts. That plan is not reported in the registry record.

Another important feature is the distinction between randomization and the analysis population. Randomization is a design strength, but analyzing a per-protocol population according to treatment received may alter the balance created by random assignment. The record’s note about treatment switching makes transparent reporting of group assignment and analysis choices particularly relevant, while leaving important details unavailable.

Finally, the record demonstrates how precision, multiplicity, and reporting completeness affect interpretation. Confidence intervals help readers see uncertainty around both percentages and risk differences. Unadjusted p-values should be read cautiously when multiple comparisons and secondary outcomes are present. The absence of a reported missing-data strategy and original sample-size justification further limits evaluation of the inferential framework. These considerations matter because statistical interpretation depends not only on the point estimates, but also on how participants, comparisons, and uncertainty were handled.

18. 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.

A central limitation is that the primary result is reported for a per-protocol population and analyzed according to treatment received rather than randomized treatment. This approach can affect comparability between groups after randomization. The record notes that 10 participants switched treatment groups, but it does not report the reasons, timing, or complete handling of those switches. An intention-to-treat analysis is not reported.

The record does not describe missing endpoint data or the methods used to handle it. Without those details, it is not possible to assess whether the reported percentages reflect all participants intended for analysis or how missing measurements might have affected the estimates. The original sample-size justification, planned primary analysis, and any interim-analysis procedures are also not reported.

Several unadjusted comparisons and secondary outcomes appear in the record, but a multiplicity strategy is not reported. This limits interpretation of individual p-values as confirmatory evidence. The posted pairwise summaries do not constitute a reported adjusted analysis, and the registry record lists no reported analyses. The confidence intervals describe sampling uncertainty under their methods, not uncertainty from every possible source of bias or analytic choice.

The four groups are all active regimens. Consequently, the comparisons do not estimate outcomes relative to placebo or no treatment. The outcome is a specific laboratory response at a defined follow-up time and should not be generalized to other endpoints without evidence. The record’s brief primary-population description is truncated after noting treatment switches, leaving some analysis details unavailable.

Finally, the registry summaries do not give enough detail to evaluate the comparative safety of the regimens. Serious adverse event counts and selected event terms are listed, but a comparative safety analysis and death counts are not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study of PEGASYS (Peginterferon Alfa-2a (40KD)) in Patients With Hepatitis Be Antigen (HBeAg) Positive Chronic Hepatitis B (CHB). — NCT00435825.
• Registry record last updated 2013-06-25; status last verified 2013-06.
• Results first posted 2013-06-25.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed, randomized, double-blind, parallel-group phase 4 study of peginterferon alfa-2a in HBeAg-positive chronic hepatitis B. It enrolled 551 participants and compared four weekly subcutaneous regimens: 90 μg or 180 μg for 24 weeks or 48 weeks. Primary completion was recorded as 2010-12.

The primary outcome was HBeAg seroconversion 24 weeks after treatment ended, defined by absence of HBeAg and presence of anti-HBe. The posted percentages ranged from 14.08% in the 90 μg, 24-week group to 36.15% in the 180 μg, 48-week group. Unadjusted pairwise risk differences and confidence intervals are reported, but the registry lists no reported analyses.

The primary population was per-protocol and analyzed according to treatment received rather than randomized treatment. Details on missing data, multiplicity, the original sample-size justification, and the full handling of treatment switches are not reported in the registry record. The results therefore describe the posted outcomes and their statistical uncertainty, with important analysis limitations.