Phase 3 Study to Evaluate the Efficacy and Safety of Elafibranor Versus Placebo in Patients With Nonalcoholic Steatohepatitis (NASH): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase 3 Study to Evaluate the Efficacy and Safety of Elafibranor Versus Placebo in Patients With Nonalcoholic Steatohepatitis (NASH) (NCT02704403), a randomized phase 3 study. The primary outcome is Number of Elafibranor-treated Participants Relative to Placebo Achieving Resolution of Nonalcoholic Steatohepatitis Without Worsening of Fibrosis.

2. Clinical Question

3. Trial Design

This was a Phase 3, multicenter, randomized, double-blind, placebo-controlled study with a parallel-group design. The registry lists quadruple masking. Elafibranor and placebo were administered as coated tablets, one tablet each day before breakfast with a glass of water. The registry records enrollment of 2157 and a study start of 2016-03. Primary completion is recorded as 2020-10-28, and the study status is terminated.

The stated study objectives included evaluating elafibranor relative to placebo for histological improvement and for all-cause mortality and liver-related outcomes in participants with NASH and fibrosis. The primary result concerns a histology endpoint at 72 weeks. Its stated population is the intent-to-treat set of randomized F2 to F3 participants who completed the Week 72 treatment period or discontinued study treatment early. This definition matters when interpreting the endpoint counts: the registry’s overall enrollment and the endpoint analysis groups describe different aspects of the study record and should not be treated as interchangeable.

The registry record does not report the original sample-size justification or the assumptions used in the trial’s design. It also does not report details about interim analyses or the full statistical analysis plan in the information summarized for this result. Those omissions limit how far the design rationale can be reconstructed from the posted result alone.

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 Set: a cohort of randomized F2 to F3 participants who completed the Week 72 treatment period or discontinued the study treatment early.

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 Number of Elafibranor-treated Participants Relative to Placebo Achieving Resolution of Nonalcoholic Steatohepatitis Without Worsening of Fibrosis, measured over Measurement at 72 weeks.

The primary endpoint counts participants who achieved resolution of NASH without worsening of fibrosis at 72 weeks. The endpoint is binary, so the posted result is a count of participants meeting the definition in each treatment group. The registry describes it as an assessment of liver histology and as a surrogate endpoint analysis. A surrogate endpoint is a measured outcome used to represent a clinical process of interest; it is not itself the same as a direct measure of mortality or another long-term clinical outcome.

The endpoint combines two conditions: NASH resolution and no worsening of fibrosis. A participant must meet the combined definition to be counted as having achieved the outcome. This makes the result interpretable as a comparison of the proportion meeting that definition in the randomized groups, although the raw arm results are recorded as counts and group sizes.

Histological improvement is one of the study’s stated objectives. The registry also names all-cause mortality and liver-related outcomes as objectives, but the primary endpoint result does not report those outcomes. The registry record does not report additional information about how biopsies were assessed, how disagreements were handled, or how the surrogate was intended to predict longer-term outcomes.

7. Results Posted in the Registry

• 120 mg Elafibranor: 19.2% (138/717) versus 14.7% (52/353) on control; risk difference 4.5 percentage points (95% CI -0.2 to 9.2), risk ratio 1.31 (0.98–1.75); unadjusted two-proportion z-test p = 0.069.

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.

Number of Elafibranor-treated Participants Relative to Placebo Achieving Improvement of Fibrosis of at Least 1 Stage

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • 120 mg Elafibranor: 24.5% (176/717) versus 22.4% (79/353) on control; risk difference 2.2 percentage points (95% CI -3.2 to 7.5), risk ratio 1.10 (0.87–1.38); unadjusted two-proportion z-test p = 0.434.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 120 mg Elafibranor and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists seven posted secondary outcomes, including histological improvement and changes in laboratory or metabolic measures. Numeric arm results are available for the fibrosis-improvement endpoint, while detailed numeric results for the other listed outcomes are not reported in the registry record in the information. The registry lists two analyses overall; it does not report sponsor analyses for the posted secondary fibrosis endpoint in the analysis details.

The secondary results should be considered alongside, not as a substitute for, the primary histology result. The primary endpoint asks whether NASH resolution occurred without worsening of fibrosis; the secondary fibrosis endpoint asks about improvement of fibrosis by at least one stage. They are related aspects of liver histology, but they are not the same endpoint and do not answer the same question. Other secondary outcomes concern different measures and should not be treated as confirmations of the primary result merely because they were assessed in the same trial.

Unadjusted secondary comparisons generally carry less evidential weight when multiple outcomes are examined. In general, testing many outcomes increases the opportunity for chance findings, and adjustment or a prespecified hierarchy can affect how results should be interpreted. The registry record does not report a multiplicity adjustment or a testing hierarchy in the information. Without that information, the secondary results should be read as exploratory or supportive evidence rather than as independently decisive conclusions. Their interpretation also depends on the endpoint definitions, analysis populations, and uncertainty estimates, which are not fully reported for all listed outcomes.

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

• Number of Elafibranor-treated Participants Relative to Placebo Achieving Improvement of Fibrosis of at Least 1 Stage
• Change From Baseline of Hemoglobin A1c (HbA1c) in Diabetic Participants After 72 Weeks of Treatment in Elafibranor-treated Participants Relative to Placebo
• Change From Baseline of High-density Lipoprotein (HDL) Cholesterol After 72 Weeks of Treatment in Elafibranor-treated Participants Relative to Placebo
• Change From Baseline of Low-density Lipoprotein (LDL) Cholesterol After 72 Weeks of Treatment in Elafibranor-treated Participants Relative to Placebo
• Change From Baseline of Homeostatic Model Assessment-IR (HOMA-IR) After 72 Weeks of Treatment in Elafibranor-treated Participants Relative to Placebo in Non-diabetic Participants
• Change From Baseline of Non-high Density Lipoprotein Cholesterol After 72 Weeks of Treatment in Elafibranor-treated Participants Relative to Placebo
• Change From Baseline of Triglycerides After 72 Weeks of Treatment in Elafibranor-treated Participants Relative to Placebo

9. Statistical Interpretation

10. Statistical Methods Explained

The endpoint is binary: participants are counted according to whether they achieved NASH resolution without worsening of fibrosis at 72 weeks. For a binary outcome, the group count is interpreted alongside the group size. The comparison can be expressed as a difference in the proportions meeting the endpoint, called a risk difference. A risk difference of zero corresponds to equal proportions; a positive value indicates a higher observed proportion in the elafibranor group, and a negative value indicates a higher observed proportion in the placebo group. These are general definitions of the measure, not claims about the biological meaning of the endpoint.

What does the unadjusted estimate describe?

The recalculated risk difference is 0.045. It is an unadjusted comparison based on the posted summary counts and group sizes. Unadjusted means that the calculation compares the groups without incorporating additional covariates in a regression model. Such a calculation is transparent and can be checked from the arm summaries, but it may not match an analysis that adjusts for other variables or uses a different model.

The registry’s own reported analysis is a logistic regression analysis, with a net mean difference of 0.043. Logistic regression is a general method for modeling a binary outcome while allowing specified explanatory variables to be included. The registry record names the method but does not report the full model specification in the information. As a result, the adjusted result should be understood as the sponsor-reported analysis, rather than assumed to be a direct reproduction of the unadjusted calculation.

How should the confidence interval be read?

A confidence interval describes the statistical uncertainty around an estimate under the assumptions of the analysis. It is not a range containing a known fixed percentage of individual participant outcomes, and it does not guarantee that the true value lies within its endpoints. In general, a wider interval indicates less precision, while a narrower interval indicates greater precision. For the unadjusted risk difference, the 95% confidence interval runs from -0.002 to 0.092. Because it includes zero, the data do not exclude a zero difference at the level represented by that interval.

The sponsor-reported interval, from -0.003 to 0.090, also includes zero. Its result is therefore consistent with the same broad reading: the estimated difference is positive, but the interval does not rule out no difference. The interval and the point estimate should be considered together rather than treating the point estimate alone as definitive.

What does a p-value add?

A p-value describes how compatible the observed data are with a specified null hypothesis, under the statistical model and its assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The unadjusted recalculation has p = 0.069, while the reported logistic regression analysis has p = 0.066. These are results from different analyses, so their small numerical difference is not evidence of a meaningful disagreement.

In general, a p-value must be interpreted alongside the estimated effect, its confidence interval, the endpoint definition, the analysis population, and the analysis plan. A threshold-based reading alone can obscure the uncertainty and scale of the estimate. The registry record does not report the full prespecified statistical plan in the information, so the status of any particular threshold or testing hierarchy cannot be established from this result alone.

Why can the estimates differ?

The unadjusted recalculation uses arm-level counts and group sizes. The sponsor’s reported result comes from logistic regression and is expressed as a net mean difference. Different estimation methods can produce slightly different point estimates, intervals, and p-values. The registry record does not provide enough model detail to explain the exact source of the numerical difference, and the values should not be treated as though they came from one identical calculation.

For this binary endpoint, the reported group counts are the number meeting the outcome definition, rather than a measure such as a mean score. General explanations about continuous-outcome methods or time-to-event methods do not change how these particular counts should be read. The registry record does not report a time-to-event analysis for this primary histology result.

Randomization is intended, in general, to support a fair comparison between groups by allocating participants without choosing their treatment based on outcome expectations. The registry records the trial as randomized. It does not, in the information summarized for this result, provide details about the randomization sequence or allocation concealment, so those procedures cannot be evaluated from the posted endpoint statistics alone.

11. Confidence Intervals and Precision

The unadjusted risk-difference estimate is 0.045, and its 95% confidence interval extends from -0.002 to 0.092. This interval includes zero and spans values on both sides of it. The result is therefore not precise enough to exclude a zero difference using this interval. At the same time, the interval has a positive upper endpoint, so the estimate is compatible with a range of positive differences as well. The interval does not identify one exact effect as certain.

The sponsor-reported logistic regression result is a net mean difference of 0.043, with a 95% confidence interval from -0.003 to 0.090. It likewise includes zero. Its endpoints are close to those of the unadjusted interval, although the analyses differ in method and effect measure. The registry record does not report enough model detail to account for each difference between the results.

In general, confidence intervals communicate both the direction and precision of an estimate. An interval that includes zero does not prove there is no effect; it indicates that the estimated data do not distinguish the zero value from the values included in the interval under the analysis assumptions. Conversely, the positive point estimate does not establish that the underlying difference is positive. Both the uncertainty and the point estimate matter.

Precision is also specific to the outcome, population, and analysis. These intervals concern the 72-week histology endpoint in the stated intent-to-treat set. They should not be taken as intervals for mortality, liver-related outcomes, other secondary endpoints, or longer-term effects. The registry record does not report confidence intervals for every other outcome in the information.

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 display is a planning illustration based on the observed effect, not a report of the study’s original design assumptions. Because these outcomes are binary participant counts rather than time-to-event outcomes, the figures are participants per arm, not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The trial’s original design assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design that would have an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true one and the assumptions held. The 90% power column gives the corresponding planning number for a higher chance of detection. These are design calculations, not observed trial outcomes. The figures are not observed power.

For the primary endpoint, the planning display gives 1,085 participants per arm for 80% power and 1,452 for 90% power when planning for 100% of the observed effect. For 75% of the observed effect, it gives 1,878 and 2,513 participants per arm; for 50% of the observed effect, it gives 4,108 and 5,499 participants per arm. The smaller target effects require more participants per arm because smaller differences are harder to distinguish from random variation under the same assumptions.

The curve and figures should be read as conditional illustrations, not as a retrospective judgment of the trial’s design or conduct. The registry record does not report the trial’s original sample-size justification, and the displayed planning exercise does not replace that missing information.

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 = 0.147; treatment proportion p₁ = 0.192; average p̄ = 0.170.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5311 = 1.0409.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5301 = 0.4462.
4. n = (1.0409 + 0.4462)² / (0.0452)² = 1,084.3, rounded up to 1,085 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 <- 0.147308781869688                          # control proportion
p1 <- 0.192468619246862                          # 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(2704403)
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 = 1,085 (80% power), 1,452 (90% power)
 75% of observed effect: n per arm = 1,878 (80% power), 2,513 (90% power)
 50% of observed effect: n per arm = 4,108 (80% power), 5,499 (90% power)
power.prop.test: 1084.3 
Simulated power at n = 1,085 per arm: 0.802 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor-reported analysis used logistic regression and reported a net mean difference of 0.043, with a 95% confidence interval from -0.003 to 0.090 and p = 0.066. The unadjusted recalculation from the posted arm summaries gives a risk difference of 0.045, with a 95% confidence interval from -0.002 to 0.092 and p = 0.069. The two point estimates and intervals are similar in broad direction and uncertainty, but the methods and reported effect measures are not identical.

The registry record names logistic regression but does not provide enough detail in the information summarized for this result to reproduce the sponsor’s model. The unadjusted calculation should therefore be treated as a check based on the posted counts, not as a replacement for the sponsor’s analysis. The sponsor’s result is the registry-reported analysis; the recalculation provides a separate, transparent comparison from the arm summaries.

Both intervals include zero. The similarity between the analyses does not remove the uncertainty reflected in their intervals, and the difference between their p-values should not be given more meaning than the methods support. The registry record does not report further model details that would establish why the exact values differ.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes or makes several statistical comparisons. In general, the more tests considered, the greater the chance that at least one result may appear notable through random variation alone. A prespecified testing hierarchy or an adjustment for multiple comparisons can help control how strongly such results are interpreted. The registry lists seven posted secondary outcomes and two analyses overall, but multiplicity procedures are not reported in the registry record in the information.

The registry record does not report whether the primary endpoint was part of a formal testing hierarchy, whether secondary endpoints were adjusted, or how any family of tests was defined. Those details matter when interpreting secondary findings and when comparing their p-values. They should not be inferred from the presence of outcome listings or from the reported primary analysis.

The primary population is described as an intent-to-treat set of randomized F2 to F3 participants who completed the Week 72 treatment period or discontinued study treatment early. This is the population definition attached to the primary histology measure. The registry record does not report additional details about how missing endpoint data were handled, whether imputation was used, or how participants without an evaluable histology assessment were treated.

The registry does not report the full statistical analysis plan, interim-analysis procedures, or sensitivity analyses in the information summarized for this result. These omissions limit assessment of whether the reported analysis followed a prespecified plan and how robust the estimate is to alternative assumptions. They do not justify guessing what those procedures may have been. The analysis population description is available, but further missing-data and multiplicity methods are not reported in the registry record.

16. Safety Results

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

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: atrial fibrillation (0.7%), arthralgia (0.7%), pneumonia (0.4%), diarrhoea (0.4%), abdominal pain (0.4%).

The registry lists serious adverse events for the safety groups as 190 affected among 1433 at risk for 120 mg elafibranor, and 95 affected among 717 at risk for placebo. It also lists other adverse events as 1227 affected among 1433 at risk for elafibranor and 601 among 717 at risk for placebo. Deaths are listed as 6 and 3, respectively. These are the posted counts and group denominators; no rates or comparative estimates are calculated.

The most frequently listed serious adverse event terms include atrial fibrillation and arthralgia, each reported as 0.7%, and pneumonia, diarrhoea, abdominal pain, and urinary tract infection, each reported as 0.4%. Those percentages are registry entries; the information does not provide further detail about their calculation or the event-level context.

Adverse-event counts are descriptive safety information. They do not by themselves establish whether an event was caused by treatment, and the counts should not be compared as though they were adjusted for differences in follow-up or other factors. The registry record does not report further safety-analysis methods in the information.

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

The primary result describes the number of participants meeting a defined histology endpoint at 72 weeks in each analysis group. The point estimate from the unadjusted comparison is positive, while the confidence interval includes zero. The sponsor-reported logistic regression analysis also has an interval that includes zero. Taken together, these statistics describe an uncertain estimate for this endpoint; they do not establish a definitive direction or magnitude of the underlying difference.

The endpoint is NASH resolution without worsening of fibrosis, not a direct report of how participants felt or functioned and not a report of mortality. The registry lists mortality and liver-related outcomes among the study objectives, but their results are not reported in the registry record with this primary result. The 72-week histology finding should therefore not be extended to outcomes that were not reported or to time periods beyond the measurement point.

The result is also specific to the stated intent-to-treat set of randomized F2 to F3 participants who completed Week 72 or discontinued treatment early. It should not automatically be generalized to populations or settings not described by that analysis population. The registry record does not provide all eligibility, missing-data, or analysis-plan details needed for a broader assessment.

In general, a confidence interval that includes zero is not proof of no effect, just as a positive point estimate is not proof of a positive effect. The uncertainty, endpoint definition, analysis method, and missing information all shape what can responsibly be said. The registry’s terminated status is relevant context, but the reason for termination is not reported in the registry record in the information. No explanation for that status should be inferred from the statistical result alone.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through its endpoint definition as well as its numerical estimate. The primary measure is a binary histology outcome that requires both NASH resolution and no worsening of fibrosis. A count of participants meeting that combined definition is not interchangeable with a different histological endpoint, a laboratory measure, or a clinical event.

It also shows the value of distinguishing a sponsor-reported adjusted analysis from an unadjusted recalculation. The posted arm summaries permit a direct risk-difference calculation, while the sponsor reports a logistic regression result. Their estimates are similar in broad terms, but the analyses are not identical. Naming the method and uncertainty avoids treating a recalculation as if it were the trial’s own analysis.

The confidence intervals are central to interpretation: both the recalculated and sponsor-reported intervals include zero. This is a useful example of why a point estimate and a p-value should not be read in isolation. The result’s statistical precision, the outcome’s clinical meaning, and the limits of the registry record all need to be considered together.

Finally, the registry lists multiple secondary endpoints and broader study objectives, while the detailed result is limited to the primary histology endpoint. Multiplicity, missing-data methods, the original design justification, and results for mortality and liver-related outcomes are not reported in the registry record in the information. Recognizing those boundaries is part of sound statistical interpretation, rather than a reason to fill gaps with assumptions.

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.

The study is recorded as terminated, but the reason is not reported in the registry record. The status alone does not explain the decision to end the study or establish whether the termination affected the endpoint results. The registry records enrollment of 2157, while the primary outcome is reported for the endpoint analysis groups of 717 and 353. The record information does not explain the relationship between the overall enrollment and those analysis-group sizes, so they should not be reconciled by assumption.

The primary endpoint population is described as randomized F2 to F3 participants who completed Week 72 or discontinued treatment early. Further details on missing histology data and the handling of participants without an evaluable endpoint are not reported in the registry record. The sponsor’s logistic regression method is named, but the full model specification is not reported in the information. This limits the ability to reproduce or fully assess the adjusted result.

The registry record also does not report the original sample-size justification, multiplicity procedures, interim analyses, or the full statistical analysis plan in the information. The planning illustration based on the observed effect is not a substitute for the trial’s original design rationale. Results for the stated mortality and liver-related objectives are not reported alongside this primary histology result, and numeric results are not available for all listed secondary outcomes.

These limitations concern what can be evaluated from the registry record. They do not establish that a particular unreported procedure was absent, nor do they resolve the reason for termination or the clinical significance of the result.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Phase 3 Study to Evaluate the Efficacy and Safety of Elafibranor Versus Placebo in Patients With Nonalcoholic Steatohepatitis (NASH) — NCT02704403.
• Registry record last updated 2022-03-23; status last verified 2022-02.
• Results first posted 2022-03-23.
• 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

NCT02704403 is a Phase 3, randomized, double-blind, placebo-controlled, parallel-group study of 120 mg elafibranor versus placebo in participants with NASH and fibrosis. The registry records quadruple masking, enrollment of 2157, a study start of 2016-03, primary completion on 2020-10-28, and terminated status.

The primary histology outcome counted participants achieving NASH resolution without worsening of fibrosis at 72 weeks. The unadjusted recalculation gives a risk difference of 0.045, with a 95% confidence interval from -0.002 to 0.092 and p = 0.069. The sponsor-reported logistic regression result is a net mean difference of 0.043, with a 95% confidence interval from -0.003 to 0.090 and p = 0.066. Both intervals include zero. The registry record does not report the reason for termination or the results for the stated mortality and liver-related objectives alongside this primary result.