VX-950-C211 - A Dosing Regimen Study (Twice Daily Versus Every 8 Hours) of Telaprevir in Treatment-naïve Participants With Genotype 1 Chronic Hepatitis C Virus Infection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for VX-950-C211 - A Dosing Regimen Study (Twice Daily Versus Every 8 Hours) of Telaprevir in Treatment-naïve Participants With Genotype 1 Chronic Hepatitis C Virus Infection (NCT01241760), a randomized phase 3 study. The primary outcome is Percentage of Participants With Sustained Virologic Response (SVR) 12 Weeks After the Last Planned Dose of Study Drugs (SVR12 Planned).

2. Clinical Question

The central contrast is between two telaprevir schedules within the same combination-treatment framework. It is not a comparison of telaprevir with no telaprevir, nor a comparison of the combination with a different treatment. The registry describes a randomized, open-label, parallel-group phase 3 study. Its stated purpose was to evaluate the effectiveness of twice-daily versus every-8-hours telaprevir when both were combined with pegylated interferon alfa-2a and ribavirin.

The primary endpoint records whether a participant met the specified virologic response criterion at the planned follow-up time. Secondary outcomes include response at other planned times, virologic failure requiring permanent discontinuation, relapse during follow-up, and response within IL28B genotype groups. The posted results also include serious adverse event counts. The registry record does not report the detailed results for every secondary outcome listed.

3. Trial Design

The study is listed as a randomized, open-label, phase 3, parallel-group trial. The registry reports enrollment of 744 participants and a completed status. The study start is recorded as 2010-12, and primary completion as 2012-08. These dates describe the record; they do not establish details of recruitment or follow-up beyond the stated endpoint timeframes.

Participants were assigned to one of two telaprevir schedules, with pegylated interferon and ribavirin in both groups. The every-8-hours regimen used telaprevir 750 mg, or 2 oral tablets, for 12 weeks. The twice-daily regimen used 1125 mg, or 3 oral tablets, every 10-14 hours for 12 weeks. Both were described as combination regimens. The registry lists no masking, so the study was open-label.

The primary outcome was planned sustained virologic response 12 weeks after the last planned dose. Its analysis population was the full analysis set: randomized participants who received at least one dose of study drug. The displayed arm sizes for this outcome are 371 for every-8-hours telaprevir and 369 for twice-daily telaprevir. The registry also reports serious adverse events for 371 and 369 participants at risk, respectively.

The registry record does not report the trial's original sample-size justification, its target effect or margin for a non-inferiority or equivalence assessment, or a detailed statistical analysis plan. It does not report whether interim analyses were planned or performed. The planning illustrations associated with the posted results are calculations based on observed effects and stated assumptions; they do not establish the assumptions used to design the trial.

4. Participant Flow and Accounting

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

Before assignment: The study was conducted between 15 November 2010 and 02 August 2012 and recruited participants from 125 study centers in 14 countries worldwide. 744 participants were initially enrolled and 740 out of them randomly allocated to the 2 treatment arms.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All analyses were performed on the full analysis (FA) set, which was defined as all randomized subjects who received at least one 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 (SVR) 12 Weeks After the Last Planned Dose of Study Drugs (SVR12 Planned), measured over End of trial, 12 weeks after last planned dose.

The primary endpoint is the percentage of participants with sustained virologic response 12 weeks after the last planned dose of study drugs, described as SVR12 planned. Response was defined by hepatitis C virus RNA levels less than 25 IU/mL. The endpoint therefore classifies participants according to whether they met a prespecified laboratory threshold at a specified follow-up time, rather than measuring a continuous change in RNA level.

A sustained response endpoint captures whether the virologic criterion was met after the planned dosing period had ended. Using the same definition and timing in both randomized groups makes the response proportions directly comparable. The endpoint is clinically relevant to the study question because the trial set out to compare dosing schedules in combination therapy, and the outcome records a virologic result following those schedules.

The registry describes the timeframe as 12 weeks after the last planned dose, at the end of the trial. The analysis population was the full analysis set, defined as randomized participants who received at least one dose of study drug. The record does not report further details about how missing endpoint measurements were handled or whether any additional rules were used to classify participants whose results were unavailable. Those details matter when interpreting a percentage because the response proportion depends not only on the outcome definition but also on the analysis population and missing-data approach.

7. Results Posted in the Registry

• T12(b.i.d.)/PR: 74.3% (274/369) versus 72.8% (270/371) on control; risk difference 1.5 percentage points (95% CI -4.9 to 7.8), risk ratio 1.02 (0.94–1.11); unadjusted two-proportion z-test p = 0.649.

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 the Last Planned Dose of Study Drugs (SVR24 Planned)

• 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:
  • T12(b.i.d.)/PR: 74.8% (276/369) versus 72.8% (270/371) on control; risk difference 2.0 percentage points (95% CI -4.3 to 8.4), risk ratio 1.03 (0.94–1.12); unadjusted two-proportion z-test p = 0.532.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between T12(b.i.d.)/PR and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Sustained Virologic Response 72 Weeks After the Start of Study Medication (SVR72 Planned)

• 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:
  • T12(b.i.d.)/PR: 70.2% (259/369) versus 69.0% (256/371) on control; risk difference 1.2 percentage points (95% CI -5.4 to 7.8), risk ratio 1.02 (0.92–1.12); unadjusted two-proportion z-test p = 0.726.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between T12(b.i.d.)/PR and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Who Relapsed During Follow-up Period

• 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:
  • T12(b.i.d.)/PR: 7.7% (23/300) versus 7.2% (21/293) on control; risk difference 0.5 percentage points (95% CI -3.7 to 4.7), risk ratio 1.07 (0.61–1.89); unadjusted two-proportion z-test p = 0.817.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between T12(b.i.d.)/PR and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary results span response at later or different planned timepoints and relapse during follow-up. Their overall pattern is similar in that the reported arm-level percentages are relatively close, and the recalculated between-group intervals include zero. This pattern is broadly consistent with the primary comparison in the limited sense that these posted estimates do not establish a clear difference between schedules. It does not show that all outcomes are equivalent, nor does it substitute for the primary endpoint's analysis.

Secondary outcomes answer distinct questions. SVR24 and SVR72 use different follow-up definitions from SVR12, while relapse is an event among participants assessed during follow-up. Their populations and denominators can differ, so comparisons across endpoints need care. The secondary outcome list also includes HCV RNA results at different time points, on-treatment virologic failure requiring permanent discontinuation, and SVR12 by IL28B genotype. Detailed results for these outcomes are not reported in the registry record.

Unadjusted secondary comparisons carry less weight as confirmatory evidence when multiple outcomes are examined. Looking across many outcomes creates more opportunities for an apparently notable result, even if each test is considered separately. The posted p-values are unadjusted; the record does not report a multiplicity strategy or specify which secondary analyses, if any, were intended as confirmatory. Secondary findings are therefore most appropriately treated as descriptive and considered alongside the endpoint definitions, estimates, and uncertainty, rather than as independent proof of a treatment difference.

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

• Percentage of Participants With Sustained Virologic Response 24 Weeks After the Last Planned Dose of Study Drugs (SVR24 Planned)
• Percentage of Participants With Sustained Virologic Response 72 Weeks After the Start of Study Medication (SVR72 Planned)
• Percentage of Participants Achieving Hepatitis C Virus (HCV) Ribonucleic Acid (RNA) Values of Less Than 25 IU/ml, Target Not Detected, at Different Time Points.
• Percentage of Participants With On-treatment Virologic Failure Which Required Them to Permanently Discontinue All Study Drugs
• Percentage of Participants Who Relapsed During Follow-up Period
• Percentage of Participants of Each IL28B Genotype Achieving Sustained Virologic Response 12 Weeks After the Last Planned Dose of Study Medication (SVR12 Planned)

9. Statistical Interpretation

10. Statistical Methods Explained

What does a response proportion describe?

A binary endpoint places each participant into one of two categories: response or no response under the registry's definition. The arm-level percentage describes the share of participants classified as responders. For the primary endpoint, response means hepatitis C virus RNA levels less than 25 IU/mL at the planned follow-up time. The percentages are easy to interpret at the group level, but they do not show how outcomes varied among individual participants or explain why a participant did or did not meet the criterion.

The displayed risk difference compares the response proportions directly. A value of zero would represent equal proportions; positive values in the posted comparison are oriented toward a higher proportion in the twice-daily group. The recalculated estimate is 0.015. This is a simple unadjusted re-calculation from posted summary statistics, not a replacement for the sponsor's analysis. No additional adjustment for participant characteristics is implied by this calculation.

What does the confidence interval add?

A confidence interval expresses the statistical uncertainty around an estimated contrast. It gives a range of values compatible with the data under the method's assumptions; it is not a guarantee that the true effect lies inside that particular interval. The primary recalculated interval runs from -0.049 to 0.078. Because the interval spans zero, the data do not distinguish the observed contrast from no difference at the conventional level associated with that interval. The interval also includes effects in both directions, so it does not rule out a potentially meaningful advantage for either schedule.

A p-value addresses a related but different question: how unusual the data would be under a specified no-difference model and the test assumptions. The primary unadjusted p-value is 0.649. It should not be read as the probability that the schedules are identical, or as the probability that the result occurred by chance. Nor does it quantify the size or clinical importance of an effect. The estimate and its interval are needed to understand magnitude and precision.

What does unadjusted mean?

The recalculated comparisons are unadjusted comparisons of the posted summary proportions. They do not incorporate a covariate-adjusted model or any additional design features that may have been used in the trial's own analysis. The sponsor's reported primary analysis is described as logistic regression, while the recalculation uses posted arm-level response counts and denominators. The registry does not provide enough detail to reconstruct the regression model or determine all of its specifications. As the record reports no discrepancy, the recalculation is best read as a transparent descriptive complement, not as a challenge to the reported analysis.

Relative measures such as risk ratios and odds ratios can express the same binary contrast on different scales. The posted recalculated comparison includes these measures, but interpretation should remain tied to the outcome definition, group sizes, and uncertainty. An odds ratio is not itself a difference in response percentages, and it should not be translated into an absolute probability without an appropriate baseline and model context.

Why do non-inferiority and equivalence require a margin?

A conventional test of difference asks whether the data are inconsistent with a zero difference. A non-inferiority assessment instead asks whether the data rule out an unacceptable loss relative to a comparator; an equivalence assessment asks whether the plausible difference lies within a defined range on either side. Both require a prespecified margin and decision rule. The registry classifies its reported analysis as non-inferiority or equivalence, but the margin and decision criteria are not reported in the registry record. Therefore, the label alone cannot establish which formal conclusion was reached.

The sponsor reports a 1.5% difference and a 95% interval from -4.9 to 12, without a reported p-value. Those numbers should be read as the posted result, not replaced by an inferred margin or an assumed interpretation. The registry record does not explain the reported interval's calculation in enough detail to independently reproduce the regression analysis.

What is the role of the analysis population?

The full analysis set includes randomized participants who received at least one dose of study drug. This definition is reported for the primary analysis. It differs from simply describing everyone enrolled, and it indicates that the endpoint results are tied to a treated, randomized population. The record does not report how many randomized participants did not receive any study drug, nor does it give detailed reasons for exclusions from the full analysis set. It also does not state how missing response measurements were handled.

These methodological details affect interpretation: the response proportion depends on who was included and how unavailable outcomes were treated. The posted group sizes and definition allow readers to identify the analysis population in broad terms, but they do not answer every question about adherence, missingness, or sensitivity analyses. Such details are not reported in the registry record.

11. Confidence Intervals and Precision

The primary recalculated risk difference is 0.015, with a 95% confidence interval from -0.049 to 0.078. The interval includes zero and extends to values on both sides of it. This means the posted data are compatible with no between-group difference as well as with differences favoring either dosing schedule. The interval is not narrow enough to support a precise estimate of the contrast.

Precision concerns the range of effects compatible with the data, not whether the point estimate looks large or small. A confidence interval is affected by the amount of information available and by the variability of the outcome. Here, the primary analysis includes 371 participants in the every-8-hours arm and 369 in the twice-daily arm. Those group sizes provide the context for the uncertainty; they do not by themselves establish that the comparison was adequately powered for a particular non-inferiority or equivalence margin.

The sponsor's reported interval for the primary comparison is 1.5%, from -4.9 to 12 at the 95% level. The registry does not report the sponsor's non-inferiority or equivalence margin, so the interval cannot be judged against such a margin from the registry record alone. A confidence interval that includes zero does not prove the schedules are identical, and a non-significant result does not establish equivalence.

The posted secondary recalculations also have intervals that include no difference. Their width varies with the outcome and available denominator, so the precision of one endpoint should not be transferred to another. For each result, the estimate, interval, endpoint definition, and analysis population should be considered together.

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 are planning calculations based on the observed effect, not the trial's original design justification. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. For these binary outcomes, the figures are participants per arm, not total participants. The registry record does not report the trial's own original sample-size assumptions.

The 80% power column indicates the number of participants per arm estimated to be needed for an 80% chance of detecting the stated effect under the planning assumptions, if that effect and those assumptions were true. The 90% power column uses a higher target chance of detection and therefore generally requires more participants per arm for the same effect. These are hypothetical design calculations, not a measure of how likely the observed result is to be correct.

Rows for 100%, 75%, and 50% of the observed effect ask what sample size would be needed if the target effect were the full observed contrast or a reduced fraction of it. Smaller effects are harder to distinguish from random variation, so planning for a smaller effect requires more participants. When the observed effect is small, the resulting planning numbers can become very large; that does not imply that the original trial had those numbers as its target.

The associated curve is another way to read the planning relationship between assumed effect and required sample size. It should be read as a sensitivity illustration under the stated assumptions, rather than as an observed trial result. These figures are 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 = 0.728; treatment proportion p₁ = 0.743; average p̄ = 0.735.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6240 = 1.2231.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6239 = 0.5251.
4. n = (1.2231 + 0.5251)² / (0.0148)² = 13,981.4, rounded up to 13,982 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 <- 0.727762803234501                          # control proportion
p1 <- 0.742547425474255                          # 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(1241760)
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 = 13,982 (80% power), 18,717 (90% power)
 75% of observed effect: n per arm = 24,968 (80% power), 33,424 (90% power)
 50% of observed effect: n per arm = 56,425 (80% power), 75,537 (90% power)
power.prop.test: 13981.4 
Simulated power at n = 13,982 per arm: 0.803 (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 the sponsor's primary analysis as logistic regression, with the parameter described as a difference in response proportions. The reported estimate is 1.5%, with a 95% confidence interval from -4.9 to 12. The analysis is classified in the record as non-inferiority or equivalence, and no p-value is reported for it.

The simple recalculation from posted arm-level results gives a risk difference of 0.015, with a 95% interval from -0.049 to 0.078 and an unadjusted p-value of 0.649. It is unadjusted and based on the posted summary counts; it is not a reconstruction of the sponsor's regression model. The registry record does not provide the model details or the margin needed to reproduce and interpret the formal analysis fully.

The record does not flag a discrepancy between the reported analysis and the recalculation. The sponsor's result should therefore be read as the trial's reported analysis, while the recalculation offers a simple summary-statistic comparison. Neither result, without the non-inferiority or equivalence margin and its decision rule, is enough to state a formal conclusion of non-inferiority or equivalence.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple secondary outcomes in addition to the primary SVR12 endpoint. The listed outcomes cover response at other planned times, HCV RNA values at different time points, on-treatment virologic failure, relapse, and SVR12 within IL28B genotype groups. Testing or interpreting many outcomes can increase the chance of finding an apparently notable result by chance. This is why prespecification and a multiplicity plan matter when distinguishing confirmatory analyses from exploratory ones.

The posted recalculated p-values are unadjusted. A multiplicity adjustment, hierarchical testing strategy, or other rule for controlling interpretation across outcomes is not reported in the registry record. The record also does not identify which secondary analyses were intended to support formal claims. Accordingly, secondary comparisons should be read as descriptive evidence, and individual unadjusted p-values should not be treated as if they were the result of a single isolated test.

The primary analysis population is defined as the full analysis set: randomized participants who received at least one dose of study drug. That definition is useful, but it does not describe all aspects of missing-data handling. The registry record does not report how participants with unavailable SVR measurements were handled, whether missing outcomes were counted as non-response, or whether sensitivity analyses examined alternative assumptions. It also does not report detailed participant flow explaining any difference between enrollment and the primary analysis group sizes.

The record does not report interim analyses, the trial's original sample-size rationale, or the complete statistical analysis plan. These omissions limit assessment of the planned analysis hierarchy, the handling of missing data, and the intended interpretation of the non-inferiority or equivalence analysis. They should be distinguished in the registry record reported: the endpoint definition, the full analysis set definition, and the posted arm-level results.

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: anaemia (3.8%), syncope (0.8%), rash (0.5%), vertigo (0.5%), thrombocytopenia (0.5%).

The serious adverse event counts are 35 participants affected among 371 at risk in the every-8-hours group and 28 among 369 at risk in the twice-daily group. The total row reports 63 affected among 740 at risk. These are counts of participants with serious adverse events, not a comparison adjusted for exposure time or other characteristics. The registry record does not report deaths for these groups.

The listed serious event terms include anaemia at 3.8%, syncope at 0.8%, and rash, vertigo, thrombocytopenia, and dehydration each at 0.5%. These percentages describe the posted term frequencies; they should not be confused with the serious-event participant counts or interpreted as a complete account of all safety outcomes. The registry record does not provide additional detail about event severity, duration, attribution, or overlap among event categories.

Counts alone do not establish whether one regimen has a different safety profile. Interpretation requires attention to definitions, follow-up, exposure, and the completeness of event reporting. The figures describe the posted serious adverse event results and do not constitute medical advice.

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

The primary endpoint results show that 72.8 of participants in the every-8-hours group and 74.3 in the twice-daily group met the registry's SVR12 definition. The recalculated contrast is small in the observed data, and its confidence interval includes zero as well as values favoring either group. The sponsor reports a difference of 1.5%, with a 95% interval from -4.9 to 12, and classifies the analysis as non-inferiority or equivalence.

These findings do not, on their own, establish that the regimens are identical or interchangeable. Failure to detect a conventional statistical difference is not evidence that there is no difference. A formal non-inferiority or equivalence interpretation depends on a specified margin and decision rule; those are not reported in the registry record. The sponsor's analysis label should not be mistaken for a fully interpretable conclusion without those details.

Nor do the posted results establish that a regimen works or does not work. The results report response under the study's definition in the analyzed participants. This is a comparison between two schedules of telaprevir, with pegylated interferon and ribavirin in both groups, rather than a comparison against no treatment or another treatment framework.

The findings also apply to the population and endpoint as recorded: treatment-naïve participants with genotype 1 chronic hepatitis C, analyzed in the full analysis set, with the primary response assessed 12 weeks after the last planned dose. The results do not automatically answer questions about other populations, other treatment combinations, or outcomes beyond those reported. The registry record leaves important details about missing outcomes, multiplicity, and the original design rationale unreported.

18. Why This Trial Matters Statistically

Statistically, the trial is useful because it directly randomized participants between two telaprevir dosing schedules while keeping the combination-treatment framework the same. That design makes the schedule contrast the focus of the primary comparison. The open-label nature and reported full analysis set definition are also relevant context for interpreting what was compared and who contributed to the endpoint analysis.

The record illustrates why an estimate should be read with its uncertainty. The primary point estimate alone gives an incomplete picture; its confidence interval includes no difference and spans possible effects in both directions. Likewise, a non-significant p-value is not a demonstration of equality. These distinctions are especially important when the reported analysis is labelled non-inferiority or equivalence, because that framework requires a margin and a decision rule.

The posted secondary outcomes offer additional views of response and relapse over different timeframes, but those endpoints are not interchangeable and their unadjusted comparisons have reduced confirmatory weight when considered across multiple outcomes. The planning illustrations also emphasize that future sample-size requirements depend on the effect a study aims to detect and the chosen power target; they are not evidence about the trial's observed power or original design.

Finally, the record provides a practical example of what registry results can and cannot establish. It gives endpoint definitions, group results, an analysis-population definition, and some safety counts, while leaving the original sample-size rationale, missing-data methods, multiplicity strategy, and non-inferiority or equivalence margin unreported. Those absences constrain formal interpretation without negating the descriptive information that is available.

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 margin or decision rule for the analysis classified as non-inferiority or equivalence. Without those details, the sponsor's reported estimate and interval cannot be judged against a prespecified acceptable difference. The regression model is named, but its specifications and other analysis details are not reported, limiting independent reproduction of the sponsor's result.

Although the primary analysis population is defined, the record does not report how missing endpoint data were handled, how many randomized participants did not receive study drug, or detailed participant flow. Such information would help clarify the consequences of the full analysis set definition and the denominators used. The original sample-size justification is also not reported, so the planning illustrations should not be mistaken for the trial's intended detectable effect or formal design requirements.

The registry does not report a multiplicity strategy for the several secondary outcomes, nor does it provide detailed results for every outcome listed. The posted unadjusted secondary comparisons therefore do not support strong confirmatory claims across all outcomes. The open-label design is reported, but the record does not describe additional procedures that might affect assessment or reporting.

The results concern treatment-naïve participants with genotype 1 chronic hepatitis C and the specific combination regimens and planned follow-up definitions recorded. They should not be generalized automatically to different populations, regimens, or outcomes. Serious adverse event counts are available, but detailed attribution, exposure-adjusted analyses, and deaths are not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: VX-950-C211 - A Dosing Regimen Study (Twice Daily Versus Every 8 Hours) of Telaprevir in Treatment-naïve Participants With Genotype 1 Chronic Hepatitis C Virus Infection — NCT01241760.
• Registry record last updated 2014-06-04; status last verified 2014-05.
• Results first posted 2014-06-04.
• 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

This completed randomized, open-label, parallel-group phase 3 study compared telaprevir given every 8 hours with telaprevir given twice daily, both in combination with pegylated interferon alfa-2a and ribavirin, in treatment-naïve participants with genotype 1 chronic hepatitis C.

The primary endpoint was SVR12, defined as hepatitis C virus RNA levels less than 25 IU/mL 12 weeks after the last planned dose. The posted response percentages were 72.8 for the every-8-hours group and 74.3 for the twice-daily group. The unadjusted recalculation yielded a risk difference of 0.015, with a 95% confidence interval from -0.049 to 0.078 and p = 0.649. The sponsor reported a difference of 1.5% with a 95% interval from -4.9 to 12.

The registry record does not report the non-inferiority or equivalence margin, the original sample-size assumptions, the missing-data approach, or a multiplicity strategy. The posted results describe the trial's observed outcomes but do not, without those details, establish equivalence or non-inferiority.