Study of Oral Treatments for Hepatitis C: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Oral Treatments for Hepatitis C (NCT02786537), a randomized phase 4 study. The primary outcome is Sustained Virologic Response (SVR12) mITT With Imputation-Phase 1 and 2 EBR/GZR, SOF/LDV.

2. Clinical Question

3. Trial Design

This was a completed, randomized, open-label, parallel phase 4 study sponsored by the University of Florida. The registry records enrollment of 1275 and a primary completion date of 2019-06-13; the study start is listed as 2016-06. Masking was none. The pragmatic design placed care, laboratory testing, and management of disease or side effects under usual-care conditions after randomization. Patient-reported outcomes were collected outside the clinic.

The treatment landscape changed during the trial. Phase 1 compared three approved DAA regimens. Phase 2 began early 2017 after removal of PrOD, leaving two approved regimens for randomization. This change matters when interpreting pooled results: Phase 1 and Phase 2 did not have the same set of randomized regimen options, and the primary outcome description combines participants from both periods for EBR/GZR and SOF/LDV, with or without ribavirin.

The registry describes four posted primary outcome arms: EBR/GZR with ribavirin, EBR/GZR without ribavirin, SOF/LDV with ribavirin, and SOF/LDV without ribavirin. Their recorded participant counts are 56, 644, 15, and 413, respectively. The corresponding SVR counts are 40, 516, 14, and 335. Ribavirin use and treatment duration were left to provider discretion, so these arm labels do not imply that every aspect of treatment was standardized by the study.

The registry does not report the original sample-size justification, the detailed randomization procedure, stratification factors, or a full statistical analysis plan. Specific allocation ratios by phase are also not reported in the registry record. Consequently, the posted aggregate results permit descriptive and unadjusted comparisons, but do not establish which design or adjustment choices were prespecified.

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: This study initially (Phase 1) randomized subjects to receive 1 of 3 HCV DAA regimens (EBR/GZR +/- RBV, LDV/SOF +/- RBV, or PrOD +/-RBV). In phase 2 of this study, randomization to PrOD regimen was discontinued and newly enrolled subjects were randomized to either EBR/GZR +/- RBV or LDV/SOF +/- RBV. Efficacy data was analyzed via original 'randomization' and as subjects were 'actually treated (regimen actually received)' while safety analysis was evaluated by actual treatment received.

As Randomized

Reasons for not completing this period:

As Treated

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: mITT with imputation, Missing SVR data = Failure. Numbers represent participants according to arm randomized (Period 1). Population excludes participants who did not start any HCV treatment.

5. Baseline Characteristics

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

Population: Study participants as randomized to HCV treatment

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Sustained Virologic Response (SVR12) mITT With Imputation-Phase 1 and 2 EBR/GZR, SOF/LDV, measured over 12 weeks post-treatment.

The primary outcome was sustained virologic response 12 weeks after treatment, abbreviated SVR12. The registry defines this as undetectable hepatitis C virus RNA at the follow-up visit 12 weeks after treatment. It also notes that the visit could occur 12 to 24 weeks after treatment discontinuation, at provider discretion. The endpoint is recorded as a count of participants, with the number in each arm who met the definition and the arm size.

As a general statistical idea, a binary endpoint such as SVR12 turns each participant’s result into one of two categories for the analysis: the endpoint was observed or it was not. This allows the trial to compare the frequency of the defined response across treatment arms. It does not by itself describe the timing or course of response between visits, and it does not summarize other outcomes such as symptoms, functional status, adherence, or adverse events.

The primary population is described as modified intention-to-treat with imputation. Participants were counted according to randomized arm, missing SVR data were counted as failure, and participants who did not start any HCV treatment were excluded. That definition is important: the reported result is not a measure of all people randomized regardless of treatment initiation, and missing follow-up is handled by a specified rule rather than omitted from the outcome definition.

7. Results Posted in the Registry

• EBR/GZR: 80.1% (516/644) versus 71.4% (40/56) on control; risk difference 8.7 percentage points (95% CI -3.5 to 20.9), risk ratio 1.12 (0.95–1.33); unadjusted two-proportion z-test p = 0.123.
• SOF/LDV With RBV: 93.3% (14/15) versus 71.4% (40/56) on control; risk difference 21.9 percentage points (95% CI 4.6 to 39.2), risk ratio 1.31 (1.06–1.62); unadjusted two-proportion z-test p = 0.077.
• SOF/LDV: 81.1% (335/413) versus 71.4% (40/56) on control; risk difference 9.7 percentage points (95% CI -2.7 to 22.1), risk ratio 1.14 (0.96–1.35); unadjusted two-proportion z-test p = 0.089.

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.

Treatment Non-Adherence Probability Estimates

• 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:
  • SOF/LDV: 19.4% (21/108) versus 23.2% (35/151) on control; risk difference -3.7 percentage points (95% CI -13.8 to 6.3), risk ratio 0.84 (0.52–1.36); unadjusted two-proportion z-test p = 0.472.
  • PrOD: 26.0% (38/146) versus 23.2% (35/151) on control; risk difference 2.8 percentage points (95% CI -6.9 to 12.6), risk ratio 1.12 (0.75–1.67); unadjusted two-proportion z-test p = 0.569.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SOF/LDV and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PrOD and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several different domains: treatment non-adherence, HCV-associated symptoms, liver disease progression or regression, functional status, adverse events leading to discontinuation, SVR durability by cirrhosis status, and the impact of baseline NS5A resistance-associated substitutions in Phase 2. The registry lists 28 outcome measures and 14 analyses overall, with 8 secondary results posted. These outcomes complement the primary virologic endpoint, but they do not all address the same question or use the same measurement scale.

The posted non-adherence summaries show arm estimates with overlapping 95% confidence intervals, and the listed unadjusted comparisons do not clearly distinguish SOF/LDV or PrOD from the EBR/GZR reference. This is a different outcome from SVR12: adherence describes treatment-taking behavior during treatment, whereas SVR12 records a post-treatment virologic outcome. The secondary adherence findings should therefore be considered alongside, not substituted for, the primary endpoint.

For the other secondary domains, detailed numerical results and comparison analyses are not reported in the registry record. Their inclusion signals that the study considered outcomes beyond SVR, but no conclusion about their direction or magnitude can be drawn from outcome titles alone. The record also does not explain whether these measures were exploratory, how missing data were managed for each one, or how results were prioritized.

Unadjusted secondary results generally carry less weight than a clearly specified primary analysis because many outcomes and comparisons create more opportunities for chance findings. As a general statistical principle, multiplicity procedures or a prespecified hierarchy can help control interpretation across repeated tests. Whether such procedures were used is not reported in the registry record. Accordingly, isolated secondary p-values should be treated as descriptive evidence, especially when the analysis plan and complete results are unavailable.

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

• Treatment Non-Adherence Probability Estimates
• Change in HCV-associated Symptoms (PROMIS Measures) After HCV Treatment Initiation
• Post-treatment Progression/Regression of Liver Disease-Fib-4
• Change in Functional Status (HCV-PRO) Within Treatment
• Number of Participants With Adverse Events That Caused Treatment Discontinuation-EBR/GZR vs. LDV/SOF
• HCV SVR Durability -No Cirrhosis
• HCV SVR Durability-Patients With Cirrhosis
• Impact of Baseline NS5A RASs on Treatment Outcomes-Phase 2

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: SVR12 is either recorded or not recorded under the endpoint definition. The posted arm counts therefore support comparisons of event frequencies. The risk difference expresses the difference between those frequencies on an absolute scale. A positive estimate indicates a higher observed frequency in the comparison arm than in the reference arm; a negative estimate would indicate a lower observed frequency. The registry comparison output also includes ratios and odds ratios, but the plain-language interpretation focuses on the absolute difference because it is directly tied to the difference in observed response frequencies.

What does an unadjusted comparison mean?

An unadjusted comparison uses the posted arm summaries without accounting for other participant or treatment characteristics. It can describe how the observed groups differ, but it cannot by itself separate treatment effects from differences in the mix of participants or care decisions. That distinction is relevant in this pragmatic study, where ribavirin and treatment duration were at provider discretion and usual care was assumed for medical management and laboratory testing. Whether the sponsor conducted adjusted analyses, and what variables those analyses used, is not reported in the registry record.

The comparison results include unadjusted p-values. In general, a p-value measures how compatible the observed data are with a specified null model; it is not the probability that a treatment effect is true, and it does not measure the size or clinical importance of a difference. Here, the p-values should be read alongside the estimated risk differences and their intervals. None of these summaries replaces a prespecified analysis plan or supplies an equivalence margin.

How should the intervals be read?

In general, an interval estimate communicates uncertainty around an estimated effect. A wider interval indicates less precision than a narrower interval, all else being equal. For a risk difference, an interval spanning zero includes the possibility of no observed difference under the interval’s assumptions. An interval entirely on one side of zero indicates that the values in that interval do not include zero, but that fact alone does not settle the importance, reliability, or clinical meaning of the result. The confidence level for the primary comparison intervals is not reported in the registry record. The secondary non-adherence outcome explicitly identifies its intervals as 95% confidence intervals.

For the primary outcome, the interval spans zero for the EBR/GZR comparison without ribavirin and for SOF/LDV without ribavirin. The interval for SOF/LDV with ribavirin lies above zero. The latter arm’s limited size makes the estimate imprecise, as reflected in its broad interval. The p-values and intervals are unadjusted summaries, and no multiplicity procedure is reported. They should not be treated as if the study had declared a single confirmatory comparison with a documented testing hierarchy.

What does the analysis population include?

The primary population is described as modified intention-to-treat with imputation. The registry specifies that missing SVR data count as failure, and that people who did not start HCV treatment are excluded. Participants are classified according to the arm randomized, which preserves randomized assignment among those included under this population definition. However, excluding people who never started treatment means the analysis does not include every randomized participant, and counting missing SVR as failure is one particular approach to incomplete outcome data. The number and reasons for missing SVR records are not reported in the registry record.

The record calls the endpoint mITT with imputation, but does not report sensitivity analyses using alternative assumptions for missing outcomes. It also does not give details about when follow-up was lost, whether missingness differed by arm, or how timing variation in the post-treatment visit was handled analytically. These omissions limit assessment of how robust the observed comparisons are to missing-data assumptions and differing follow-up schedules.

Why does the pragmatic setting matter?

Pragmatic trials assess outcomes in care conditions intended to resemble routine practice. As a general concept, this can make results informative about what happens when clinicians and patients make treatment decisions within ordinary care, but it can also introduce variation in treatment delivery and outcome collection. In this study, providers determined ribavirin use and course duration, and usual care assumed responsibility for clinical management and testing after randomization. Patient-reported outcomes were collected outside the clinic. The registry does not report the exact methods for ensuring comparable outcome ascertainment across arms or sites.

The design changed between phases, with PrOD removed from Phase 2. The posted primary result combines eligible EBR/GZR and SOF/LDV participants across phases, while the secondary outcome list includes a Phase 2-specific outcome concerning baseline NS5A resistance-associated substitutions. Phase-related differences could affect interpretation, but phase-specific primary effect estimates are not reported in the registry record. Nor are there reported details on phase-specific allocation, adjustment for phase, or an interaction analysis.

Finally, the posted arm comparisons are not enough to infer that ribavirin itself caused differences. Ribavirin was used at provider discretion, and the direct comparisons listed use EBR/GZR with ribavirin as reference rather than a documented randomized ribavirin assignment. The registry record does not report a separate causal analysis of ribavirin use. Interpretation should therefore stay close to the randomized regimen arms and the recorded summaries, without extending the estimates to unreported comparisons.

11. Confidence Intervals and Precision

Precision varies across the posted primary comparisons. The EBR/GZR with ribavirin reference arm contains 56 participants, compared with 644 in the EBR/GZR arm without ribavirin, 15 in the SOF/LDV arm with ribavirin, and 413 in the SOF/LDV arm without ribavirin. The SOF/LDV with ribavirin estimate is based on the smallest arm, so its interval is broad. That interval lies above zero, but its width signals uncertainty about the magnitude of the difference.

The intervals for the EBR/GZR and SOF/LDV arms without ribavirin include zero. Their estimates therefore allow a range of possibilities that includes no difference as well as differences in either direction. The intervals are not all equally precise, and a single direction of the point estimates should not obscure that uncertainty. The registry comparison output does not state the confidence level for these primary intervals, so a confidence level should not be assumed from the record alone.

For treatment non-adherence, the secondary outcome explicitly reports 95% confidence intervals. EBR/GZR is reported at 23% with an interval from 17% to 29%; SOF/LDV is 19% with an interval from 10% to 27%; and PrOD is 26% with an interval from 19% to 33%. The unadjusted risk-difference intervals for the SOF/LDV and PrOD comparisons each include zero. These results leave substantial uncertainty about the differences between arms.

In general, precision depends on the amount of information in the data, including the number of participants and how frequently the outcome occurs. A large arm does not automatically make every comparison precise if its reference arm is small, and an estimate from a small arm can be especially sensitive to individual outcomes. Interval width is therefore important alongside the point estimate. It conveys what the data can and cannot distinguish, without showing that the true effect must equal the point estimate.

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 use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They calculate the number of participants per arm for binary outcomes, using the stated fraction of the observed effect as the effect to detect. The registry does not report the trial’s original sample-size assumptions or justification; these figures are planning illustrations based on observed results, not the design target used to launch the study.

The 80% power column means the planning calculation targets an 80% chance of detecting the specified effect under its assumptions if that effect were the true one. The 90% power column uses a higher target chance of detection and consequently requires more participants per arm for the same effect. These are hypothetical design calculations, not observed power.

For example, planning around 100% of the observed EBR/GZR risk-difference estimate gives 380 participants per arm for 80% power and 509 participants per arm for 90% power. Planning for 75% of that observed effect gives 697 and 932 participants per arm, respectively; planning for 50% gives 1,613 and 2,158 participants per arm. Smaller effects need more participants because they are harder to distinguish from ordinary sampling variation. The illustrations use equal allocation even though the observed arm sizes are unequal. They should be read as sensitivity to assumed effect size, not as evidence that the trial had a particular power or that a future trial will reproduce the observed effect.

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 = 0.714; treatment proportion p₁ = 0.801; average p̄ = 0.758.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6059 = 1.1875.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6028 = 0.5073.
4. n = (1.1875 + 0.5073)² / (0.0870)² = 379.9, rounded up to 380 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 <- 0.714285714285714                          # control proportion
p1 <- 0.801242236024845                          # 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(2786537)
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 = 380 (80% power), 509 (90% power)
 75% of observed effect: n per arm = 697 (80% power), 932 (90% power)
 50% of observed effect: n per arm = 1,613 (80% power), 2,158 (90% power)
power.prop.test: 379.9 
Simulated power at n = 380 per arm: 0.797 (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 identifies a primary SVR12 outcome and lists multiple secondary outcomes, but the planned approach to multiplicity is not reported in the registry record. It is not stated whether the investigators adjusted for multiple comparisons, used a hierarchical testing strategy, designated particular secondary outcomes as confirmatory, or treated the secondary analyses as exploratory. Without those details, unadjusted p-values should not be interpreted as if they came from a single protected family of tests.

The posted primary comparison p-values are unadjusted. The listed secondary non-adherence comparisons are also unadjusted. The record does not provide a full accounting of all analyses performed or clarify how the posted tests relate to the 28 outcome measures and 14 analyses recorded. A complete analysis plan, including prespecified contrasts and decision rules, is not reported in the registry record.

Missing primary SVR data were handled by counting missing outcomes as failures, according to the mITT-with-imputation description. Participants who did not start HCV treatment were excluded from this population, while participants who started treatment were counted according to their randomized arm. The number of missing SVR outcomes, reasons for missingness, and sensitivity analyses under alternative assumptions are not reported in the registry record. Thus, the stated rule is clear, but the extent and potential impact of missing data cannot be assessed from the posted information.

Details about missingness and analysis populations for the secondary outcomes are also not reported. The registry does not give outcome-specific denominators or describe whether all randomized participants contributed to each secondary analysis. The primary endpoint population should not be assumed to apply automatically to every secondary outcome.

These gaps do not erase the posted counts, but they constrain how strongly the comparisons can be interpreted. In general, multiplicity and missing-data methods are part of what defines the inferential meaning of results, rather than technical details that can be inferred from p-values alone.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: neuroendocrine carcinoma (1.8%), papillary thyroid cancer (1.8%), chest pain (1.0%), completed suicide (1.0%), drug abuse (1.0%).

The safety record reports serious adverse events, other adverse events, and deaths by group. For serious adverse events, the posted affected counts are 30 of 664 for EBR/GZR, 2 of 56 for EBR/GZR with ribavirin, 0 of 15 for SOF/LDV with ribavirin, 6 of 394 for SOF/LDV, 5 of 99 for PrOD with ribavirin, and 0 of 47 for PrOD. These are descriptive group counts; the record does not provide a randomized or adjusted comparison of safety between regimens.

Other adverse events were reported in 298 of 664, 46 of 56, 8 of 15, 184 of 394, 74 of 99, and 32 of 47 participants in those respective groups. The death counts were 6, 0, 0, 4, 1, and 0. These outcomes should be kept distinct: the count of participants with a serious event is not the same as the count with any other reported adverse event, and a death count does not establish its cause or relationship to treatment.

The registry lists serious-event terms including neuroendocrine carcinoma and papillary thyroid cancer at 1.8% each, and chest pain, completed suicide, drug abuse, and osteomyelitis at 1.0% each. The record does not give enough context to infer causality, compare event rates reliably, or determine whether these terms occurred during treatment or afterward. Safety counts describe reported events in the registry and should not be read as proof that a regimen caused an event.

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

The primary result is a comparison of observed SVR12 counts under the study’s pragmatic care conditions. The posted counts show that SVR was recorded in each of the four arms, with varying arm sizes and outcome counts. The unadjusted comparisons estimate differences relative to EBR/GZR with ribavirin; their intervals and p-values indicate that the estimates are not equally precise and do not provide a consistent basis for declaring the regimens equivalent or different across all contrasts.

The record’s endpoint definition and population rule are central to the result. Missing SVR data were treated as failure, and people who did not start HCV treatment were excluded. The data therefore describe the outcome under that analysis definition, not an unrestricted analysis of every randomized participant. Provider discretion over ribavirin and treatment duration also means that the observed arms represent treatment as delivered in practice rather than a fully fixed treatment course.

The trial’s pragmatic design gives context to outcomes collected during usual care, but it also means that clinical management and testing were not all controlled by a uniform study protocol after randomization. The registry does not report phase-specific primary effects, detailed adjusted analyses, missing-data sensitivity analyses, or the full statistical plan. Those omissions prevent a more complete assessment of how robust the comparisons are to differences in participant mix, phase, care, and follow-up.

These posted results do not establish that a treatment works or does not work, and they do not determine which treatment is appropriate for any person. A statistical comparison is not a medical recommendation. Nor does a nonsignificant unadjusted p-value demonstrate equivalence; that would require a suitable design and a prespecified margin, neither of which is reported in the registry record. The result is best understood as a set of observed arm outcomes and uncertain unadjusted contrasts, interpreted within the registry’s stated population and follow-up definitions.

17. Why This Trial Matters Statistically

This trial is statistically notable because it combines randomized allocation with pragmatic delivery. Randomization supports comparison of assigned regimens, while usual-care decisions about ribavirin and treatment duration preserve flexibility in how care was delivered. That combination makes it especially important to distinguish the randomized regimen comparison from associations involving treatment choices made by providers.

The design also changed over time: Phase 1 included three regimen options, and Phase 2 removed PrOD from randomization. The primary outcome description pools eligible EBR/GZR and SOF/LDV participants across both phases. When trial options change, phase and treatment availability can matter for interpretation. The registry does not report phase-specific primary estimates or the methods used to account for phase, so readers should not assume the pooled contrasts represent identical treatment contexts throughout the study.

Unequal arm sizes and the small SOF/LDV-with-ribavirin arm illustrate why a point estimate alone is not enough. Interval width and the reference group size affect how much confidence to place in a contrast. The differing results also demonstrate that failure to show a clear difference is not proof of equivalence, particularly without a documented equivalence or noninferiority framework.

Finally, the study includes outcomes beyond SVR, such as adherence, patient-reported measures, liver disease markers, and safety. Their presence reflects a broader view of treatment outcomes, but interpretation depends on complete results, a prespecified analysis plan, and transparent handling of multiplicity and missing data. Several of those details are not reported in the registry record. The statistical value of the record is therefore strongest when its posted counts are read descriptively and its inferential limits are kept explicit.

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.

Several trial-specific features limit interpretation of the posted comparisons. First, the treatment options changed between phases: PrOD was available only in Phase 1, while Phase 2 included two regimens. The primary outcome description combines Phase 1 and Phase 2 participants for EBR/GZR and SOF/LDV, but phase-specific effect estimates and phase-adjusted analyses are not reported in the registry record.

Second, ribavirin use and treatment duration were at provider discretion. The posted arms distinguish use of ribavirin, but the registry does not describe a randomized ribavirin assignment or report an analysis designed to isolate ribavirin’s effect. Comparisons between those arms should not be treated as causal estimates of adding ribavirin.

Third, the primary population excludes participants who did not start treatment and counts missing SVR as failure. The number and reasons for missing outcomes, as well as sensitivity analyses, are not reported. The outcome visit could occur 12 to 24 weeks after treatment discontinuation at provider discretion, so timing was not described as a single fixed interval for every participant.

Fourth, the primary comparisons are unadjusted, and a detailed sponsor analysis is not reported in the registry record. The confidence level for the primary comparison intervals, the multiplicity strategy, and the original sample-size justification are also not reported. Finally, although the registry lists numerous secondary domains, detailed numerical findings are not available for all of them. These limitations leave uncertainty about generalizability, phase effects, missing-data robustness, and the interpretation of multiple comparisons.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study of Oral Treatments for Hepatitis C — NCT02786537.
• Registry record last updated 2021-12-06; status last verified 2021-12.
• Results first posted 2020-11-24.
• 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.

22. Record Summary

NCT02786537 is a completed randomized, open-label, parallel phase 4 study of oral regimens for chronic hepatitis C, sponsored by the University of Florida. Enrollment was 1275. The primary outcome was SVR12, defined as undetectable HCV RNA at follow-up 12 weeks after treatment, with the visit permitted 12 to 24 weeks after discontinuation at provider discretion. The primary population used missing-equals-failure imputation and excluded participants who did not start treatment.

The posted primary results give SVR counts for four EBR/GZR and SOF/LDV arms, with or without ribavirin. Unadjusted comparisons use EBR/GZR with ribavirin as the reference. The record also includes safety counts and secondary outcome information, including treatment non-adherence, but detailed results for several secondary domains are not reported. The original sample-size justification, full statistical analysis plan, multiplicity strategy, and primary confidence-interval confidence level are not reported in the registry record.