An Efficacy, Pharmacokinetics, Safety and Tolerability Study of TMC435 as Part of a Treatment Regimen for Hepatitis C-Infected Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for An Efficacy, Pharmacokinetics, Safety and Tolerability Study of TMC435 as Part of a Treatment Regimen for Hepatitis C-Infected Patients (NCT01725529), a randomized phase 3 study. The primary outcome is Percentage of Participants With Sustained Virologic Response 12 Weeks After End of Study Drug Treatment (SVR12).

2. Clinical Question

The trial asks whether adding TMC435 to peginterferon alfa-2a and ribavirin is associated with a different rate of sustained virologic response than adding placebo to the same background regimen in treatment-naïve participants with genotype 1 hepatitis C. The registry describes two TMC435 doses, so the primary outcome is compared separately for the 100 mg and 150 mg groups against placebo.

3. Trial Design

This was a Phase III, randomized, double-blind, placebo-controlled, parallel-group study. The registry lists quadruple masking and an enrollment of 457. The study is recorded as completed, with a start date of 2012-11 and primary completion in 2014-08. Janssen R&D Ireland is named as sponsor.

Three treatment groups are represented in the outcome results: placebo, simeprevir (TMC435) 100 mg, and simeprevir (TMC435) 150 mg. The active-treatment descriptions specify TMC435 once daily for 12 weeks with peginterferon alfa-2a and ribavirin, followed by the background medicines alone. Response-guided criteria determined whether the active-treatment groups had a total treatment duration of 24 or 48 weeks. The control group received placebo with the background medicines for 48 weeks.

Randomization assigns participants to treatment groups by chance. In general, this supports comparisons between groups by reducing the risk that treatment choice is systematically related to participant characteristics, although it does not guarantee that every characteristic is balanced. Blinding is intended to limit the influence of treatment knowledge on participant care, reporting, and assessment. The registry does not report further details about how randomization was implemented, which people were masked, or whether allocation was stratified.

The primary outcome population is described as intent-to-treat and includes randomized participants who took at least 1 dose of study drug. The results list 152 participants for placebo, 153 for the 100 mg group, and 152 for the 150 mg group. The registry record does not report a separate account of withdrawals or the handling of participants with missing endpoint information. The trial's original sample-size justification and its detailed statistical analysis plan are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT) population included all the randomized participants who took at least 1 dose of study drug.

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 Sustained Virologic Response 12 Weeks After End of Study Drug Treatment (SVR12), measured over 12 weeks after the end of treatment (EOT: Week 24 or 48).

The primary endpoint is the percentage of participants with sustained virologic response 12 weeks after the end of study drug treatment, called SVR12. The registry defines the end of treatment as Week 24 or 48. To count as having achieved SVR12, a participant had to meet both stated conditions: hepatitis C virus RNA was below the lower limit of quantification, 25 international units per milliliter, and undetectable at the end of treatment; and HCV RNA was below that limit, whether detectable or undetectable, 12 weeks after the planned end of study drug treatment.

This endpoint uses a laboratory measure of viral RNA at a specified follow-up point rather than a symptom or clinician judgment. Sustained response is used to assess whether the endpoint criterion is met after treatment has ended. The endpoint's definition also makes timing important: participants could have different planned treatment end points, at Week 24 or 48, while the response assessment was tied to the planned end of treatment.

The registry reports the outcome as a percentage and identifies the primary population as the intent-to-treat population, defined as randomized participants who took at least 1 dose of study drug. The record does not describe how missing RNA measurements were classified, or provide a separate per-protocol or other population result. Those details matter when interpreting a percentage, because they determine which participants contribute to its numerator and denominator.

7. Results Posted in the Registry

• Simeprevir (TMC435) 100mg: 88.9% (136/153) versus 75.7% (115/152) on control; risk difference 13.2 percentage points (95% CI 4.8 to 21.7), risk ratio 1.17 (1.06–1.31); unadjusted two-proportion z-test p = 0.002.
• Simeprevir (TMC435) 150mg: 90.8% (138/152) versus 75.7% (115/152) on control; risk difference 15.1 percentage points (95% CI 6.9 to 23.4), risk ratio 1.20 (1.08–1.33); 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 Sustained Virologic Response 24 Weeks After End of Study Drug Treatment (SVR24)

• 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:
  • Simeprevir (TMC435) 100mg: 88.9% (136/153) versus 75.0% (114/152) on control; risk difference 13.9 percentage points (95% CI 5.4 to 22.4), risk ratio 1.19 (1.06–1.32); unadjusted two-proportion z-test p = 0.002.
  • Simeprevir (TMC435) 150mg: 90.8% (138/152) versus 75.0% (114/152) on control; risk difference 15.8 percentage points (95% CI 7.5 to 24.1), risk ratio 1.21 (1.09–1.34); 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 Simeprevir (TMC435) 100mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Simeprevir (TMC435) 150mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Sustained Virologic Response at Week 72 (SVRW72)

• 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:
  • Simeprevir (TMC435) 100mg: 87.6% (134/153) versus 75.0% (114/152) on control; risk difference 12.6 percentage points (95% CI 3.9 to 21.2), risk ratio 1.17 (1.05–1.30); unadjusted two-proportion z-test p = 0.005.
  • Simeprevir (TMC435) 150mg: 90.1% (137/152) versus 75.0% (114/152) on control; risk difference 15.1 percentage points (95% CI 6.8 to 23.5), risk ratio 1.20 (1.08–1.34); 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 Simeprevir (TMC435) 100mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Simeprevir (TMC435) 150mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With On-treatment Failure

• 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:
  • Simeprevir (TMC435) 100mg: 3.3% (5/153) versus 12.5% (19/152) on control; risk difference -9.2 percentage points (95% CI -15.2 to -3.3), risk ratio 0.26 (0.10–0.68); unadjusted two-proportion z-test p = 0.003.
  • Simeprevir (TMC435) 150mg: 3.3% (5/152) versus 12.5% (19/152) on control; risk difference -9.2 percentage points (95% CI -15.2 to -3.2), risk ratio 0.26 (0.10–0.69); unadjusted two-proportion z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Simeprevir (TMC435) 100mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Simeprevir (TMC435) 150mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the primary SVR12 assessment to later response time points and other aspects of treatment outcome. The posted SVR24 and Week 72 response percentages follow the same broad direction as the primary endpoint, with higher response percentages in both active groups than in the placebo group. The posted on-treatment failure results show the opposite-direction pattern, with lower percentages in the active groups than in placebo. Together, these outcomes are directionally consistent with the primary comparison rather than presenting an obvious reversal across the reported endpoints.

That overall pattern is supportive context, not a replacement for the primary endpoint. SVR24 and SVRW72 assess response at different times, while on-treatment failure captures a different event during treatment. Their definitions and timing are not interchangeable with SVR12. Concordance can make the results easier to interpret as a coherent set, but it does not establish that all outcomes were prespecified, independently confirmed, or analyzed under a multiplicity-controlled plan.

The registry lists six secondary outcome measures, including viral breakthrough, viral relapse, and on-treatment normalization of alanine aminotransferase. Numeric results for those measures are not reported in the registry record. The numerical secondary results available include SVR24, SVRW72, and on-treatment failure. No sponsor-reported secondary analyses are listed.

Unadjusted secondary results carry less inferential weight when many outcomes or comparisons are examined. In general, repeated testing increases the chance that at least one comparison will appear unusual by chance, even when there is no corresponding underlying effect. A prespecified testing hierarchy or adjustment can address this issue, but neither is reported in the registry record. The secondary pattern is therefore best treated as descriptive and complementary to the primary result, rather than as a collection of independent confirmatory conclusions.

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

• Percentage of Participants With Sustained Virologic Response 24 Weeks After End of Study Drug Treatment (SVR24)
• Percentage of Participants With Sustained Virologic Response at Week 72 (SVRW72)
• Percentage of Participants With On-treatment Failure
• Percentage of Participants With Viral Breakthrough
• Percentage of Participants With Viral Relapse
• Percentage of Participants With On-treatment Normalization of Alanine Aminotransferase Level

9. Statistical Interpretation

10. Statistical Methods Explained

The main outcome is binary at the participant level: each participant either meets the stated SVR12 definition or does not. The results are reported as percentages by group. The comparisons use risk differences, which express the difference between the event proportions in two groups. Here, the active-treatment group is compared separately with placebo. The recalculated contrasts are unadjusted comparisons based on posted summary counts.

What does a risk difference represent?

In general, a risk difference compares the proportion with an outcome in one group with the proportion in another group by subtraction. A value above zero means the outcome proportion is higher in the group placed first in the comparison; a value below zero means it is lower. In this trial, the reported positive primary risk differences indicate higher SVR12 proportions in each TMC435 group than in placebo. The estimates should be read with their intervals, because a single point estimate does not show how uncertain the comparison is.

How should the p-values be read?

The primary comparisons have unadjusted p-values of 0.002 for the 100 mg group and <0.001 for the 150 mg group. In general, a p-value measures how unusual data at least as incompatible with a specified null model would be if that model were true, under the test's assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The registry record does not report the test used to obtain sponsor-reported p-values or a prespecified threshold for the trial's primary analysis. The posted p-values are unadjusted recalculations, so they do not account for testing multiple comparisons.

What information does the denominator give?

The primary results list 152 participants for placebo, 153 for TMC435 100 mg, and 152 for TMC435 150 mg. The endpoint description says the intent-to-treat population includes randomized participants who took at least 1 dose of study drug. Group denominators are essential context for percentages: the same percentage can arise from different numbers of participants, and the amount of information available depends in part on how many observations contribute. The registry record does not state how missing endpoint data were treated or whether the denominators reflect any exclusions after the intent-to-treat population was defined.

Why use intervals as well as point estimates?

In general, an interval estimate shows uncertainty around an estimated effect, rather than presenting the estimate as exact. A narrower interval indicates greater precision for that estimate under the method used; a wider one indicates less precision. The posted primary comparisons include lower and upper limits, but the confidence level and interval calculation method are not reported in the registry record. These limits should therefore be described as the posted intervals rather than assigned an unstated confidence level.

What does randomization contribute?

In general, random assignment helps make treatment groups comparable in expectation and supports an interpretation of between-group differences as associated with assigned treatment. Masking can reduce the influence of treatment knowledge on some aspects of trial conduct and assessment. Those design features do not remove the need to examine outcome definitions, missing observations, adherence, and analysis choices. Details about randomization procedures, adherence analysis, and missing-data methods are not reported in the registry record.

What is the role of the secondary outcomes?

Secondary outcomes examine other endpoints or time points, including response at later follow-up and on-treatment failure. They can add context about the pattern of results, but multiple outcomes create more opportunities for chance findings. In general, prespecified multiplicity control can help address that issue. A multiplicity adjustment or a hierarchy for secondary outcomes is not reported in the registry record, and no sponsor-reported analyses are listed for the secondary results.

Planning calculations are distinct from analysis of the trial's observed outcomes. The posted planning illustration uses an assumed significance level, allocation, approximation, and effect size fraction; it does not establish the assumptions used for the original trial design. The sample-size interpretation describes planning scenarios only and should not be confused with the trial's observed group results or with an observed-power calculation.

11. Confidence Intervals and Precision

The primary risk-difference interval for the 100 mg comparison runs from 0.048 to 0.217 around an estimate of 0.132. For the 150 mg comparison, it runs from 0.069 to 0.234 around an estimate of 0.151. Both intervals lie above zero, while their widths indicate that the exact size of the difference remains uncertain. The registry record does not state the confidence level or interval method, so neither should be inferred from the listed limits.

In general, an interval is a way to express the range of estimates that remain reasonably compatible with the observed data under a specified procedure. It is not a guarantee that the true value lies inside the particular reported interval, and it is not a measure of the probability that the treatment effect has a given value. Wider intervals generally indicate less precision; narrower intervals generally indicate more precision. These principles are general statistical explanations, not additional trial findings.

The group sizes are 152, 153, and 152. The interval widths should be interpreted in light of the number of participants and the binary nature of the outcome: the amount of information depends on both the group sizes and the observed event proportions. The registry record does not report a separate precision analysis, the handling of missing measurements, or a confidence level for these recalculated intervals. Consequently, the interval limits are useful for conveying uncertainty, but they do not answer questions about the choice of method or the effect of any missing outcome data.

The p-values of 0.002 and <0.001 are also unadjusted. They are not measures of precision and do not replace the intervals. A small p-value can coexist with substantial uncertainty about the exact effect size. The clinical importance of a particular risk difference cannot be determined from the statistical interval alone; the registry record does not state a threshold for a clinically important difference.

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 event counts. The planning illustration is based on a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as a reference and considers planning for 100%, 75%, or 50% of that observed effect. These are planning assumptions for the illustration, not the trial's original design assumptions. The original sample-size justification is not reported in the registry record.

The 80% power column gives the per-arm sample size that the stated planning calculation associates with an 80% chance of detecting the specified effect, if the assumptions used in that calculation hold. The 90% power column gives the corresponding per-arm size for a 90% chance under those assumptions. Power is a property of a planned test under an assumed effect and model; it does not describe the probability that the observed result is true.

The rows that plan for a smaller fraction of the observed effect require more participants per arm than rows planning for the full observed effect. This follows the general principle that smaller differences are harder to distinguish from random variation, all else equal. The numeric requirements differ by endpoint and comparison, so each scenario should be read as its own planning illustration, rather than as a single enrollment target for the study.

These figures are not observed power. They are not a retrospective assessment of whether the completed study had enough participants, and they do not establish what the trial's original investigators assumed. The total enrollment of 457 is a separate registry fact; the planning calculations should not be read as evidence that the trial was designed using these calculations.

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 = 0.757; treatment proportion p₁ = 0.889; average p̄ = 0.823.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5401 = 1.0585.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5319 = 0.4477.
4. n = (1.0585 + 0.4477)² / (0.1323)² = 129.6, rounded up to 130 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 <- 0.756578947368421                          # control proportion
p1 <- 0.888888888888889                          # 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(1725529)
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 = 130 (80% power), 173 (90% power)
 75% of observed effect: n per arm = 248 (80% power), 332 (90% power)
 50% of observed effect: n per arm = 595 (80% power), 796 (90% power)
power.prop.test: 129.6 
Simulated power at n = 130 per arm: 0.806 (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 reports two primary active-versus-placebo comparisons, one for each TMC435 dose, and several secondary outcomes. The primary recalculated p-values are unadjusted. The registry record does not report whether the trial's original analysis controlled the family-wise error rate or used another multiplicity procedure, nor whether one dose comparison was designated as the main contrast. Without that information, the p-values should not be interpreted as multiplicity-adjusted evidence across the set of comparisons.

Multiplicity matters because the chance of at least one low p-value can increase when multiple hypotheses are tested. In general, adjusting for multiple testing or specifying an ordered testing strategy can help keep the interpretation aligned with the planned questions. That general concern is relevant to both the pair of dose comparisons and the range of secondary outcomes. It does not, by itself, determine whether any particular result is valid; the missing information is about the analysis strategy and its prespecification.

The primary population is identified as intent-to-treat participants who were randomized and took at least 1 dose of study drug. The posted arm denominators are available, but the registry record does not report a missing-data method, the amount or pattern of missing endpoint data, or how participants with missing HCV RNA results were classified. It also does not report sensitivity analyses that could show how alternative assumptions about missing outcomes might affect the results.

Randomization and masking are reported, but detailed analysis-population definitions beyond the primary population are not. The registry record does not report a per-protocol analysis or a separate as-treated analysis. The posted summary therefore supports interpretation of the reported group percentages and unadjusted recalculations, but it does not answer every question about protocol deviations, adherence, missingness, or confirmatory analysis choices. Those uncertainties should be kept distinct from the observed endpoint pattern.

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: craniocerebral injury (0.7%), foot fracture (0.7%), meniscus lesion (0.7%), multiple injuries (0.7%), rib fracture (0.7%).

The serious adverse event results list 9 affected participants among 152 at risk in the placebo group, 5 among 153 at risk in the TMC435 100 mg group, and 5 among 152 at risk in the TMC435 150 mg group. These are group counts, not evidence on their own that an event was caused by a study treatment. The registry also lists 149 participants with other adverse events in each group, with at-risk group sizes of 152, 153, and 152, respectively.

The listed serious adverse event terms include craniocerebral injury, foot fracture, meniscus lesion, multiple injuries, rib fracture, and tibia fracture, each reported as 0.7%. The record does not provide further event-level detail in these results, such as timing or attribution. Death counts are not reported in the registry record. The counts describe the posted safety data; they should be interpreted alongside the study's population, exposure, and event definitions, details that are not fully available in the registry record.

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

The posted primary results show higher SVR12 percentages in both TMC435 groups than in the placebo group. The unadjusted risk-difference estimates are positive, and the posted intervals for both comparisons lie above zero. These statistics describe the observed results and their uncertainty using the recalculated comparisons; they do not determine whether a difference is clinically important or establish the effect in a different setting.

The randomized, double-blind, placebo-controlled design is relevant to interpreting between-group differences. Random assignment supports comparison of groups as allocated, and masking can reduce some sources of bias. However, the registry record does not provide the detailed analysis plan, missing-data handling, or multiplicity procedure needed to assess all analysis decisions. The posted results are not a substitute for those details.

The endpoint is specifically defined by HCV RNA measurements around the end of treatment and at follow-up. It should not be broadened into claims about outcomes that were not measured in this primary endpoint. Nor does the primary result answer every question about safety, durability beyond the recorded assessment, or effectiveness in populations unlike the treatment-naïve genotype 1 participants described in the registry.

Statistical estimates describe how the observed groups compare under the reported definitions. In general, causal interpretation depends on design and analysis assumptions, including the treatment assignment process and outcome ascertainment. The record documents randomization and masking, but does not report every detail needed to assess those assumptions. The results therefore support a focused interpretation of this trial's endpoint and groups, rather than a universal conclusion about treatment.

The endpoint percentages, risk differences, intervals, and p-values answer different questions. Percentages describe outcomes in each group; risk differences summarize the contrast; intervals convey uncertainty around that contrast; and p-values assess compatibility with a null model under a test's assumptions. None alone gives a complete account. The registry record also does not state a threshold for clinical importance, so statistical evidence should not be equated with a judgment about the practical meaning of the difference.

17. Why This Trial Matters Statistically

This trial illustrates how a randomized comparison can report both group-level outcome proportions and direct contrasts between groups. The percentages make the observed endpoint frequency interpretable within each arm, while the risk differences place the two active-versus-placebo comparisons on a common scale. Presenting uncertainty intervals alongside those estimates helps distinguish an estimated effect from its precision.

The two active doses also make clear why comparisons should be understood in context rather than reduced to a single favorable result. Each dose has its own estimate and interval against the shared placebo group. Those comparisons are not independent replications, and the registry record does not report an adjustment for considering them together. The secondary response and failure outcomes add context, but their unadjusted status and missing analysis details limit confirmatory interpretation.

The record demonstrates the importance of separating the trial's observed results from planning illustrations. The sample-size scenarios use fractions of the observed effect under stated assumptions, whereas the trial's original sample-size justification is not reported. A planning calculation can show how desired power and assumed effect size relate to participant requirements, but it cannot establish the design choices made for this completed study or measure its observed power.

Finally, the endpoint definition and population definition matter as much as the statistical contrast. SVR12 is tied to specified HCV RNA criteria and follow-up timing, and the primary population is defined as randomized participants who took at least 1 dose. Clear interpretation depends on retaining those boundaries and recognizing where the registry record does not report details, especially for missing data, multiplicity, and the analysis plan.

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.

The registry record does not report the original sample-size justification, so the planning illustration cannot be used to reconstruct the trial's design assumptions. It also does not report the detailed statistical analysis plan, including the test and interval methods used for the posted comparisons, a multiplicity strategy, or a hierarchy for primary and secondary hypotheses. The unadjusted recalculations should be interpreted with those omissions in mind.

The primary population definition is stated, but methods for missing endpoint measurements are not. The record does not give the amount or pattern of missing HCV RNA data, how missing values were classified, or sensitivity analyses. It also does not report adherence information or results for alternative analysis populations. These omissions limit assessment of how robust the percentages are to analysis-population choices.

Although six secondary outcome measures are listed, numeric results are not reported in the registry record for viral breakthrough, viral relapse, or on-treatment normalization of alanine aminotransferase. The posted numerical secondary results cover SVR24, SVRW72, and on-treatment failure. The study title includes pharmacokinetics, safety, and tolerability, but detailed pharmacokinetic results are not reported in the registry record summarized by these outcomes. Death counts are also not reported.

The record describes quadruple masking and randomization but does not provide implementation details, such as the allocation procedure or any stratification factors. It does not report detailed event-level safety information or attribution. These are limitations of the available registry reporting, not evidence that a particular design or analysis procedure was or was not used.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: An Efficacy, Pharmacokinetics, Safety and Tolerability Study of TMC435 as Part of a Treatment Regimen for Hepatitis C-Infected Patients — NCT01725529.
• Registry record last updated 2015-08-13; status last verified 2015-07.
• Results first posted 2015-08-13.
• 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

This completed Phase III randomized, double-blind, placebo-controlled parallel-group trial enrolled 457 treatment-naïve participants with genotype 1 hepatitis C. Participants received placebo or TMC435 100 mg or 150 mg alongside peginterferon alfa-2a and ribavirin. The primary endpoint was SVR12, defined using HCV RNA criteria at the end of treatment and 12 weeks after the planned end.

Posted SVR12 percentages were 75.7% with placebo, 88.9% with TMC435 100 mg, and 90.8% with TMC435 150 mg. Unadjusted recalculated risk differences versus placebo were 0.132 and 0.151, respectively. The registry record does not report the original sample-size justification, detailed analysis plan, multiplicity method, or missing-data handling.