Peg-Intron/Ribavirin in G 1 HCV for Non-Extended Versus 24 Week Extended Treatment After 24 Weeks (Study P04144)(COMPLETED): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Peg-Intron/Ribavirin in G 1 HCV for Non-Extended Versus 24 Week Extended Treatment After 24 Weeks (Study P04144)(COMPLETED) (NCT00202839), a randomized phase 4 study. The primary outcome is The Percentage of Participants Who Achieved a Sustained Virologic Response (SVR).

2. Clinical Question

The central contrast is between treatment durations, not between combination therapy and no therapy: both groups received 24 weeks of treatment before randomization. The registry describes the study as randomized and open-label. The primary endpoint is a binary participant-level outcome, classified according to whether the specified virologic response was achieved.

3. Trial Design

This was a phase 4, randomized, open-label, parallel-group study of peginterferon alfa-2b and ribavirin in genotype 1 chronic hepatitis C. The registry describes a multicenter study and records 160 participants enrolled. The study began in 2005-03, reached primary completion in 2008-07, and is listed as completed.

All participants first completed 24 weeks of pilot treatment. Eligible participants were then randomly assigned to either stop study medication or continue the combination for an additional 24 weeks. The 24-week treatment group had no further study medication after randomization and was followed for an additional 48 weeks. The 48-week treatment group received medication for 24 more weeks and then had 24 weeks of follow-up without study medication.

The primary endpoint was assessed 24 weeks after treatment ended in each group. This means the time from randomization to the primary assessment differed according to assigned treatment duration, while the endpoint was anchored to the end of treatment. The registry also lists virologic response 48 weeks after randomization as a secondary outcome.

The study is described as open-label, so participants and study personnel were not masked to treatment assignment. The registry record does not report details of sequence generation, allocation concealment, stratification, or the criteria determining eligibility for randomization after the pilot period. The original sample-size justification and the trial’s prespecified statistical analysis plan are not reported in the registry record. Those omissions limit assessment of how the study was planned and how all planned analyses relate to 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention to treat \[ITT\] population defined as participants who received at least one dose of study medication.

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 The Percentage of Participants Who Achieved a Sustained Virologic Response (SVR), measured over 24 weeks of follow-up after either 24 or 48 weeks of anti-HCV therapy.

The primary endpoint is the percentage of participants who achieved sustained virologic response. The registry defines this as HCV-RNA below assay detection 24 weeks after termination of anti-HCV therapy. It is a binary outcome for each participant: the response criterion was either met or not met at the specified follow-up assessment.

A sustained response measured after treatment has ended is used to distinguish a response that persists through follow-up from a result measured during treatment. The endpoint therefore combines a laboratory criterion with a defined timing relative to the end of medication. Its interpretation depends on both parts of that definition, as well as on whether participants had outcome information available at the assessment.

The registry’s primary analysis population is intention to treat, defined in the record as participants who received at least one dose of study medication. The posted group percentages describe the proportion meeting the response criterion in each assigned treatment group. They do not by themselves describe the timing or pattern of individual HCV-RNA measurements, reasons for any missing assessment, or later clinical outcomes. Those details are not reported in the registry record.

7. Results Posted in the Registry

• 48-Week Treatment: 67.1% (55/82) versus 56.4% (44/78) on control; risk difference 10.7 percentage points (95% CI -4.3 to 25.6), risk ratio 1.19 (0.93–1.52); unadjusted two-proportion z-test p = 0.165.

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.

The Percentage of Participants Who Achieved a Virologic Response 48 Weeks After Randomization.

• 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:
  • 48-Week Treatment: 67.1% (55/82) versus 57.7% (45/78) on control; risk difference 9.4 percentage points (95% CI -5.6 to 24.3), risk ratio 1.16 (0.91–1.48); unadjusted two-proportion z-test p = 0.221.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 48-Week Treatment and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary outcome: virologic response 48 weeks after randomization. Its pattern is broadly consistent with the primary outcome in that the point estimate favors the 48-week treatment group. The interval for the secondary risk difference includes zero, so it does not provide a clear separation between the groups. The secondary finding therefore does not resolve the uncertainty in the primary comparison.

The secondary assessment is related to the primary endpoint but uses a different time reference: it is measured 48 weeks after randomization, whereas the primary response is assessed 24 weeks after treatment ends. This timing difference matters because the groups had different treatment durations after randomization. The secondary result is useful as an additional description of outcome patterns, but it should not be treated as a duplicate primary analysis or as independent confirmation.

The registry reports no multiplicity adjustment for secondary analyses. When multiple outcomes or comparisons are examined, the chance of finding an apparently notable result by chance can increase. Unadjusted secondary results therefore carry less weight than a prespecified primary result, especially when they are related to that primary endpoint. The record does not provide a broader list of planned secondary analyses or an analysis hierarchy, so the full context for multiplicity cannot be assessed.

The secondary outcome’s unadjusted comparison is based on the same treatment groups and a similar binary response measure. Its direction adds descriptive context, but its uncertainty and relationship to the primary outcome mean that it does not establish a separate treatment effect.

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

• The Percentage of Participants Who Achieved a Virologic Response 48 Weeks After Randomization.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a percentage, meaning the count of participants meeting the response definition divided by the number assessed in a treatment group. For a binary endpoint, each participant contributes to one of two outcome categories. A percentage is easy to interpret, but its precision depends in part on how many participants contribute information and how the outcomes are distributed.

What does the risk difference express?

The risk difference compares the response proportion in the 48-week group with the proportion in the 24-week group. A value above zero indicates a higher observed proportion in the 48-week group; a value below zero indicates a lower observed proportion. The reported primary estimate is 0.107. This is an unadjusted contrast based on the posted summary counts, rather than an estimate adjusted for other participant characteristics.

A risk difference keeps the comparison on the scale of the outcome proportions. Other measures, such as a risk ratio or odds ratio, express the same binary comparison on different scales. The registry record includes recalculated relative measures, but the risk difference is the most direct way to describe an absolute separation in response proportions. These measures do not remove uncertainty or resolve the limitations of the design and reporting.

How should the p-value be read?

The unadjusted p-value is 0.165, and the sponsor-reported chi-squared analysis has p = 0.165. In general, a p-value measures how unusual data at least as incompatible with the null hypothesis as those observed would be, if the null hypothesis and the test assumptions held. It is not a measure of effect size, clinical importance, or the probability that a treatment difference is real.

The chi-squared test is a general method for comparing categorical outcome distributions. Its use reflects the binary response and two treatment groups. The registry does not report additional detail about the exact implementation of the test, such as whether it used a continuity correction. The close agreement between the reported result and the unadjusted recalculation is consistent with the absence of a recorded discrepancy; the sponsor’s reported result remains the trial’s own analysis.

What does a confidence interval add?

A confidence interval presents a range of estimates compatible with the observed data under the method’s assumptions. The primary risk-difference interval is -0.043 to 0.257. Since it includes zero, it includes the value corresponding to no difference in response proportion. The interval also includes values on either side of zero, so the data do not precisely establish the direction or magnitude of the difference.

In general, a confidence interval is not a statement that there is a specified probability that the fixed underlying effect lies within the particular interval. Its repeated-sampling interpretation concerns the method used to construct intervals across studies conducted under the same assumptions. The registry reports a 95% confidence level for the sponsor’s chi-squared analysis; estimates and intervals should be read in the context of the methods used to obtain them.

Why does the analysis population matter?

The registry defines the primary intention-to-treat population as participants who received at least one dose of study medication. That definition is narrower than a general description of all people who might have been enrolled, and it does not by itself explain how participants were handled if they were randomized but had no dose or lacked an endpoint measurement. The record does not report missing-data rules or the number of participants with missing primary outcome information.

Because randomization occurred after the pilot treatment period among eligible participants, the comparison concerns those who reached the randomization stage and met the eligibility requirements. The registry does not provide a full flow of participants through enrollment, pilot treatment, eligibility, randomization, and outcome assessment. That flow would help readers judge how exclusions and missing observations might affect the comparison.

What is the role of the planning illustration?

The planning figures are illustrations based on the observed effect, not the original trial’s design calculation. They assume a two-sided significance level of 0.05, equal allocation between groups, and a normal approximation. Each scenario uses a stated fraction of the observed effect. For the primary outcome, the figures range from 325 participants per arm for planning for 100% of the observed effect to 1,334 participants per arm for planning for 50% of the observed effect at 80% power. The corresponding figures at 90% power are 435 and 1,786 participants per arm. The intermediate scenario plans for 75% of the observed effect.

These scenarios illustrate how assumptions about the effect and desired power influence planning; they do not recover the trial’s original design assumptions. The registry does not report the original sample-size justification. The planning calculations are not observed power and should not be used as a retrospective measure of whether the study result is true.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.107, with an interval from -0.043 to 0.257. This interval is wide enough to include both a negative difference and a positive difference. Because it includes zero, it does not rule out no difference under the interval’s assumptions. The estimate’s direction is not settled by the data with high precision.

Confidence intervals are useful because they show a range of effect values compatible with the observed result, not just a single estimate. A point estimate can appear clear while its interval reveals that the data are consistent with a range of possible effects. The interval should not be read as proving that every value within it is equally likely, or that values outside it are impossible.

The secondary risk-difference estimate is 0.094, with an interval from -0.056 to 0.243. It too includes zero and extends to both negative and positive differences. The similar direction of the two point estimates does not eliminate uncertainty, particularly because the outcomes are related and the registry does not report multiplicity adjustment.

Group sizes were 78 and 82 for the primary outcome. These numbers help explain why estimates from this study are less precise than the large per-arm numbers in the planning illustrations. The registry does not report a confidence interval for each group’s percentage; the comparison interval is the relevant measure of uncertainty for the difference between groups. Missing outcome information and its handling are not reported in the registry record, so the effect of missingness on precision cannot be assessed from the record.

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 figures are participants per arm, not total events. They are illustrations based on the observed primary effect rather than the original sample-size calculation for the trial. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each scenario targets a stated fraction of the observed effect.

For planning for 100% of the observed effect, the illustration gives 325 participants per arm for 80% power and 435 participants per arm for 90% power. For planning for 75% of the observed effect, it gives 586 and 784 participants per arm, respectively. For planning for 50% of the observed effect, it gives 1,334 and 1,786 participants per arm, respectively.

In general, power is the probability that a study will detect an effect of a specified size under the assumed statistical model, if that effect is present. The 80% and 90% columns describe different planning targets for that probability; the higher target requires more participants under the same other assumptions. Smaller effects are harder to distinguish from random variation, so planning for smaller effects requires more participants.

These values are not observed power. They are prospective planning illustrations, and their estimates depend on the assumed effect size and calculation method. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

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 = 0.564; treatment proportion p₁ = 0.671; average p̄ = 0.617.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6873 = 1.3471.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6832 = 0.5750.
4. n = (1.3471 + 0.5750)² / (0.1066)² = 324.9, rounded up to 325 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 <- 0.564102564102564                          # control proportion
p1 <- 0.670731707317073                          # 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(202839)
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 = 325 (80% power), 435 (90% power)
 75% of observed effect: n per arm = 586 (80% power), 784 (90% power)
 50% of observed effect: n per arm = 1,334 (80% power), 1,786 (90% power)
power.prop.test: 324.9 
Simulated power at n = 325 per arm: 0.800 (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 reports a sponsor analysis using a chi-squared method, with p = 0.165 and a 95% confidence level recorded for that analysis. An unadjusted recalculation from the posted summary statistics gives p = 0.165. The record does not flag a discrepancy, and the values are close.

The recalculation is a simple comparison of the posted group summaries, not a replacement for the sponsor’s own analysis or a reconstruction of any unreported adjusted model. The sponsor’s reported result is the trial’s analysis as recorded. The registry does not report additional adjustment details or other modeling choices that would allow a more extensive comparison of methods.

Both values indicate that the observed data do not provide strong evidence against the null hypothesis under the respective tests. Neither p-value describes the probability that the treatment groups are equivalent, and neither establishes the size or clinical importance of a difference. The effect estimate and its confidence interval remain important for understanding direction and precision.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary sustained virologic response outcome and a secondary virologic response outcome at 48 weeks after randomization. It reports one analysis for the primary comparison and no analysis entries for the secondary outcome. The record does not report whether the investigators prespecified a hierarchy among outcomes, planned multiple subgroup analyses, or adjusted for multiplicity.

Multiplicity arises when several hypotheses are tested. With more opportunities to test for differences, an apparently unusual result can occur by chance more often than it would in a single prespecified test. Adjustment procedures or a prespecified testing hierarchy can address this issue, but the registry record does not state whether either was used. The secondary result should consequently be treated as supportive description rather than definitive evidence.

The primary population is described as intention to treat and defined as participants who received at least one dose of study medication. The record does not report how participants with missing primary endpoint data were handled, whether any were excluded from the analysis, or whether sensitivity analyses were performed. It also does not give a full participant flow through the pilot-treatment eligibility assessment and randomization.

These reporting gaps matter because the interpretation of a randomized comparison depends on who was included and how missing outcomes were addressed. The available description gives the stated population definition and group denominators, but it does not establish that every randomized participant had an observed outcome or explain any departure from the stated analysis population. Details of the original statistical analysis plan, including prespecification and missing-data methods, are not reported in the registry record.

16. 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: cholelithiasis (2.4%), nodule (1.3%), cholecystitis (1.3%), tonsillitis (1.3%), head injury (1.3%).

The registry lists serious adverse events affecting 5 participants in the 24-week treatment group, with 78 at risk, and 8 participants in the 48-week treatment group, with 82 at risk. It lists other adverse events affecting 29 participants in the 24-week group and 47 in the 48-week group, with the same group sizes at risk. These are participant counts, not event rates calculated for comparison.

The serious-event terms listed most often include cholelithiasis at 2.4%; nodule, cholecystitis, tonsillitis, head injury, and limb injury are each listed at 1.3%. The registry does not provide enough detail in these figures to attribute a particular event to treatment duration or to compare event severity beyond the serious-event classification.

Deaths are not reported in the registry record. The adverse-event counts are descriptive and should be interpreted with the study’s group sizes and reporting limits in mind. They do not, by themselves, establish a comparative safety effect.

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

The posted results describe a randomized comparison of two treatment durations among eligible genotype 1 chronic hepatitis C participants who had completed the pilot treatment period. The response percentages were higher in the 48-week group than in the 24-week group, and the estimated risk difference points in that same direction. The confidence interval nevertheless includes zero, leaving uncertainty about whether a difference exists and about its size.

These results do not establish that the longer treatment duration improves outcomes, nor do they establish that the two durations are equivalent. A non-significant comparison is not proof of no effect. The study’s outcome and population also limit what can be inferred: the primary result concerns a laboratory-defined response at a specified follow-up time, not every aspect of health or longer-term outcome.

The randomized design supports comparison of assigned groups among those reaching randomization, but the open-label conduct and incomplete reporting of participant flow and missing-data handling should be considered. The study enrolled 160 participants overall, with 78 and 82 in the primary outcome groups. The intervals indicate that estimates remain imprecise in this study.

In general, statistical interpretation combines the observed effect, its precision, study design, endpoint definition, and reporting quality. A p-value alone cannot answer whether a difference is important, and a point estimate alone cannot show how reliably it has been estimated. The registry record does not report the original sample-size justification, detailed statistical plan, or missing-data procedures, all of which would help put the results in context.

The secondary outcome follows a similar direction but does not settle the uncertainty and carries less evidential weight in the absence of reported multiplicity handling. Safety counts are also descriptive. Together, the registry results offer information about observed outcomes in this study, but they do not support a definitive claim about treatment effectiveness or comparative safety.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares treatment duration after a common initial treatment period. That design focuses the randomized contrast on whether participants continued combination therapy after the pilot period, rather than comparing treatment with no initial treatment. The primary outcome is defined at a consistent interval after treatment termination, while the secondary outcome uses a fixed time after randomization.

The contrast illustrates why endpoint timing should be read alongside treatment assignment. Since post-randomization treatment duration differed between groups, the time from randomization to the primary assessment was not the same, even though the primary assessment followed treatment termination by the same interval. The distinction helps clarify what each endpoint estimates.

The analysis also illustrates the value of considering effect estimates and confidence intervals together. The observed point estimate favors one group, but the interval includes no difference and spans effects in either direction. The p-value alone would conceal that range of plausible values. The registry’s reported and recalculated p-values are close, while neither makes the estimate more precise.

Finally, the record exposes the importance of statistical reporting. Information about the original sample-size calculation, participant flow, missing outcomes, and multiplicity would help readers assess the planned and executed analyses. Without those details, interpretation must stay close to the posted comparison and acknowledge that some aspects of the analysis cannot be evaluated.

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 registry record does not report the original sample-size justification, so it is not possible to determine what effect the trial was designed to detect or what assumptions informed its enrollment target. The planning illustrations based on the observed effect are not substitutes for that missing design information.

Participant flow is incompletely described. The record states that eligible participants were randomized after the 24-week pilot period and defines the primary population as participants who received at least one dose of study medication, but it does not give a full account of eligibility, randomization, exclusions, or outcome availability. Missing-data methods and sensitivity analyses are not reported in the registry record.

The registry labels the study open-label. It does not report allocation-concealment details or the procedures used to standardize outcome assessment. The laboratory definition of sustained response is specified, but the record does not provide details about assay procedures or how results below assay detection were handled beyond the endpoint definition.

The record provides one secondary outcome and does not report whether multiple-testing adjustments or a formal testing hierarchy were planned. It also does not include detailed adverse-event analyses that would support a formal comparison of safety between treatment groups. These limitations constrain interpretation of the posted estimates and the completeness of the statistical assessment.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Peg-Intron/Ribavirin in G 1 HCV for Non-Extended Versus 24 Week Extended Treatment After 24 Weeks (Study P04144)(COMPLETED) — NCT00202839.
• Registry record last updated 2017-04-06; status last verified 2017-03.
• Results first posted 2011-03-24.
• 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 describes a completed, phase 4, randomized, open-label, parallel-group study of peginterferon alfa-2b plus ribavirin in genotype 1 chronic hepatitis C. After 24 weeks of pilot treatment, eligible participants were assigned to stop treatment or continue for 24 additional weeks. The primary endpoint was sustained virologic response 24 weeks after treatment ended.

The posted response percentages were 56.41% with 24-week treatment and 67.07% with 48-week treatment. The primary risk-difference interval includes zero, and the reported chi-squared p-value is 0.165. The secondary outcome follows a similar direction but also remains uncertain. Original design assumptions, missing-data handling, and multiplicity procedures are not reported in the registry record.