Study Evaluating the Efficacy and Safety of Obeticholic Acid in Subjects With Compensated Cirrhosis Due to Nonalcoholic Steatohepatitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study Evaluating the Efficacy and Safety of Obeticholic Acid in Subjects With Compensated Cirrhosis Due to Nonalcoholic Steatohepatitis (NCT03439254), a randomized phase 3 study. The primary outcome is DB Phase: Number of Participants Who Were Responders and Showed Improvement in Fibrosis by at Least 1 Stage Without Worsening of Nonalcoholic Steatohepatitis (NASH).

2. Clinical Question

The question combines a tissue-based measure of fibrosis with a condition that steatohepatitis must not worsen. It is therefore not simply a question about a change in a laboratory value or about fibrosis considered in isolation. The outcome is a binary responder classification: each participant either met the stated criteria or did not. The posted primary results count responders in each study group.

The registry describes fibrosis staging using the NASH Clinical Research Network fibrosis staging system. Its definition of no worsening refers to lobular inflammation and hepatocellular ballooning, assessed using relevant categories of the nonalcoholic fatty liver disease activity score. The score also includes steatosis, but the responder condition described in the record specifically names the inflammation and ballooning grades.

Interpretation must account for the additional responder conditions. Participants who discontinued because of an adverse event, died, or lacked an evaluable post-baseline biopsy do not satisfy the stated responder definition. The registry record does not report further details about how these situations were handled in the analysis beyond that definition. The results consequently describe the recorded responder classification, rather than an isolated change in fibrosis stage among all participants regardless of follow-up or biopsy availability.

3. Trial Design

NCT03439254 is recorded as a completed phase 3 trial sponsored by Intercept Pharmaceuticals. The study enrolled 919 participants and was randomized, quadruple-masked, placebo-controlled, multicenter, and parallel-group. The official title describes a double-blind study, while the registry’s masking field specifies quadruple masking. The design compared placebo with OCA 10 mg and with an OCA regimen that began at 10 mg and could be titrated up to 25 mg.

The registry lists the study start as 2017-08-30 and primary completion as 2022-09-08. The treatment descriptions specify up to 18 months in the double-blind phase. In the titration group, the description says that participants received 10 mg during the first 3 months and could then titrate up to 25 mg for the remaining 15 months. The record does not give further detail about the criteria governing titration.

The primary endpoint is a binary count of participants meeting the fibrosis-response definition without worsening of NASH. The outcome population is identified as the ITT Population, and the primary timeframe is up to 18 months. The posted counts are 31.0 responders among 313.0 in the placebo group, 33.0 among 296.0 in the OCA 10 mg group, and 37.0 among 310.0 in the titrated OCA group. These are the registry’s reported arm summaries; the counts should be read with the endpoint definition and the analysis population in mind.

The registry also lists secondary outcomes involving change from baseline to Month 18 in liver stiffness measurement (LSM), and baseline FIB-4 and ELF. Numerical secondary summaries in the record cover baseline FIB-4 and ELF. The record does not report a numerical result for the listed LSM change outcome in the information analyzed. Original design assumptions, including the trial’s own sample-size justification and planned statistical analysis details, are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: This was a Phase 3, double-Blind, randomized, placebo-controlled, multicenter study to evaluate the efficacy and safety of Obeticholic Acid (OCA) in participants with compensated cirrhosis due to Nonalcoholic Steatohepatitis (NASH). The study comprised of a double-blind (DB) phase (18 months) followed by Open-label extension (OLE) phase (12 months).

Double-blind Phase (18 Months)

Reasons for not completing this period:

Open Label Extension Phase (12 Months)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT Population.

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: Intent-To-Treat (ITT) Population: included all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as DB Phase: Number of Participants Who Were Responders and Showed Improvement in Fibrosis by at Least 1 Stage Without Worsening of Nonalcoholic Steatohepatitis (NASH), measured over Up to 18 months.

The primary endpoint counts participants who were classified as responders: they had improvement in fibrosis by at least 1 stage, without worsening of NASH, and met the additional conditions in the registry definition. Specifically, the definition excludes participants who discontinued treatment because of an adverse event or died, and requires an evaluable post-baseline biopsy assessment. The endpoint is described for the ITT Population and assessed over up to 18 months.

Fibrosis stage was evaluated with the NASH Clinical Research Network fibrosis staging system. The record defines no worsening of steatohepatitis as no worsening in lobular inflammation or hepatocellular ballooning grade, according to the relevant categories of the nonalcoholic fatty liver disease activity score. That score is a semiquantitative measure based on steatosis, lobular inflammation, and hepatocellular ballooning; the record describes a total scale range from 0 to 12, with higher scores representing worse symptoms.

A combined endpoint can be useful when the clinical question requires improvement in a target feature without deterioration in another aspect of the disease. Here, the response rule asks for fibrosis improvement while guarding against worsening in specified NASH features. At the same time, collapsing these conditions into a responder count loses detail: the binary result does not show the amount of fibrosis change, the separate pattern of the NASH components, or how participants who fail one part of the rule differ from those who meet it. The posted count is therefore best understood as the frequency of meeting this particular composite responder definition, not as a full description of each participant’s tissue findings.

7. Results Posted in the Registry

• DB: OCA 10 Milligrams (mg): 11.1% (33/296) versus 9.9% (31/313) on control; risk difference 1.2 percentage points (95% CI -3.6 to 6.1), risk ratio 1.13 (0.71–1.79); unadjusted two-proportion z-test p = 0.617.
• DB: OCA 10 mg Titrated to OCA 25 mg: 11.9% (37/310) versus 9.9% (31/313) on control; risk difference 2.0 percentage points (95% CI -2.9 to 6.9), risk ratio 1.21 (0.77–1.89); unadjusted two-proportion z-test p = 0.416.

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.

DB Phase: FIB-4 at Baseline

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • DB: OCA 10 Milligrams (mg): mean 2.48 versus 2.28 on control; difference 0.20 (95% CI -0.06 to 0.45), standardized effect d = 0.13; z-test p = 0.128.
  • DB: OCA 10 mg Titrated to OCA 25 mg: mean 2.40 versus 2.28 on control; difference 0.13 (95% CI -0.05 to 0.31), standardized effect d = 0.11; z-test p = 0.168.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DB: OCA 10 Milligrams (mg) 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 DB: OCA 10 mg Titrated to OCA 25 mg and the control. The interval gives the range of effects that remain compatible with the data.

DB Phase: ELF at Baseline

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • DB: OCA 10 Milligrams (mg): mean 10.60 versus 10.50 on control; difference 0.10 (95% CI -0.05 to 0.25), standardized effect d = 0.11; z-test p = 0.183.
  • DB: OCA 10 mg Titrated to OCA 25 mg: mean 10.61 versus 10.50 on control; difference 0.11 (95% CI -0.03 to 0.25), standardized effect d = 0.12; z-test p = 0.128.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DB: OCA 10 Milligrams (mg) 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 DB: OCA 10 mg Titrated to OCA 25 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering LSM change from baseline to Month 18, baseline FIB-4, and baseline ELF. Numerical secondary summaries available in the record describe the baseline FIB-4 and ELF measures; a numerical result for the listed LSM change outcome is not reported in the registry record analyzed. The baseline measures provide context about the groups at the start of the double-blind phase. They are not evidence of a change during treatment.

Across the posted baseline summaries, the group means are in a broadly similar range, while the standard deviations show within-group variation. The recalculated mean differences for these baseline measures have confidence intervals that include zero. These are descriptive comparisons at baseline, not efficacy comparisons. Their role is different from the primary outcome, which measures whether participants met the fibrosis-response definition over the study period.

The primary and secondary outcomes are related through the overall disease-assessment context, but they answer different questions. The primary endpoint is a defined responder count combining fibrosis improvement and no worsening of specified NASH features. Baseline FIB-4 and ELF describe starting measurements, while the listed LSM outcome concerns change during follow-up. A pattern in baseline measures cannot establish or explain a treatment effect on the primary endpoint, and unavailable numerical LSM results cannot be inferred from the other measures.

Secondary analyses generally carry less evidential weight when many outcomes or comparisons are examined without a reported multiplicity strategy. Repeated testing increases the chance that some estimates appear notable by chance. The registry record does not report a multiplicity adjustment or hierarchy that establishes how secondary findings should be prioritized. It also does not report the planned analysis details for these secondary outcomes. Accordingly, secondary results are best treated as supporting or descriptive information, rather than as independent confirmation of the primary result. Any unadjusted secondary p-values, if considered, would need this context; no unreported result should be inferred.

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

• DB Phase: Change From Baseline to Month 18 in LSM
• DB Phase: FIB-4 at Baseline
• DB Phase: ELF at Baseline

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary count represent?

The outcome is a binary response classification. A participant either met the stated criteria or did not, and the registry reports the number classified as responders in each arm. A count alone does not express the comparison between groups, so a contrast such as a risk difference or response ratio is used to describe how the responder frequencies compare. The posted arm counts and denominators provide the basic context for those comparisons.

The responder definition is composite. It requires improvement in fibrosis by at least 1 stage and no worsening of specified NASH features. It also requires an evaluable post-baseline biopsy and excludes participants who discontinued treatment because of an adverse event or died. The outcome therefore combines disease assessments with follow-up and treatment-status conditions. The record does not report a separate component analysis that would show which part of the definition most often determined response status.

How should a risk difference be read?

A risk difference is the response proportion in the OCA group minus the response proportion in the placebo group. A positive estimate means the recorded response proportion is higher in the OCA group on this scale; a negative estimate means it is lower. Zero represents no difference between the two proportions. This is a general explanation of the measure. The recalculated estimates are unadjusted contrasts from the posted summary statistics, not the sponsor’s reported analysis.

A risk difference is expressed on an absolute scale. It describes the gap in response frequency rather than a proportional change relative to the comparator. The estimate is accompanied by a confidence interval to convey statistical uncertainty. Because the intervals in both primary comparisons span zero, the posted summary statistics are compatible with a range that includes no difference. The interval limits also indicate that the estimates are not precise enough to establish a tightly bounded contrast.

What does the response ratio describe?

The registry’s reported analyses use Cochran-Mantel-Haenszel estimates of response ratios. A response ratio compares the response frequency in an OCA arm with the response frequency in the placebo arm on a relative scale. A value of 1 corresponds to equal response frequencies; values above or below 1 represent relative differences in either direction. These are general definitions of the measures. The sponsor-reported point estimates and their intervals are stated separately from the unadjusted recalculated risk differences because the two scales answer related but not identical questions.

The registry identifies the method as Cochran-Mantel-Haenszel, but does not report the stratification variables, model details, or other implementation information in the record analyzed. A method name alone is not enough to reconstruct every aspect of an analysis. The sponsor’s reported response ratios should therefore be read as the registry’s own analysis results, without assuming unreported details about how the method was implemented.

What do confidence intervals and p-values add?

A confidence interval is a range of estimates compatible with the observed data under the statistical procedure and its assumptions. It displays both the direction and the precision of an estimate. A wide interval indicates substantial uncertainty; a narrow interval indicates greater precision. In general, the interval is not a range that contains a fixed proportion of individual participant outcomes, nor does it give the probability that the true effect lies inside its particular limits.

A p-value summarizes how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the analysis assumptions held. It does not measure the size of an effect or establish whether a result matters clinically. Here, the registry reports p-values for its response-ratio analyses, and unadjusted p-values accompany the recalculated risk differences. The distinct methods and measures explain why the figures need not match exactly.

Why can over-dispersion matter?

Over-dispersion is a general issue in count and proportion data when the observed variability is greater than a model assumes. If a method assumes less variability than the data contain, uncertainty can be understated; a model that accounts for extra variability can produce more cautious uncertainty estimates. The primary outcome is a participant count with a binary responder classification, rather than a continuous measurement. The registry record does not report an over-dispersion assessment or a model-based over-dispersion adjustment for this endpoint, so it would not be appropriate to claim that one was used or needed.

How should the baseline continuous measures be treated?

FIB-4 and ELF are reported as baseline means with standard deviations. A standard deviation describes variability among observations within a group; it is not the uncertainty around the group mean. The recalculated comparisons are unadjusted differences between the posted group means. Since these entries describe baseline measurements, they characterize the groups at the start of the double-blind phase rather than showing change caused by assigned treatment. A difference at baseline cannot be interpreted as a treatment effect.

For continuous measures, the registry record does not provide sponsor-reported analyses alongside the posted baseline summaries. Any recalculated mean differences are simple comparisons based on the posted summary statistics. They should not be read as adjusted estimates or substitutes for an analysis that might account for the trial’s design or other covariates.

What statistical details remain unavailable?

The registry record does not report the trial’s original sample-size justification, its original design assumptions, a prespecified analysis plan in enough detail to reproduce the analyses, or the approach to multiplicity across outcomes and comparisons. It also does not report further details about missing-data methods or sensitivity analyses. Those omissions limit independent assessment of whether the posted analyses match the full prespecified plan, and they prevent conclusions about unreported procedures. General statistical explanations in this discussion describe concepts, not undocumented features of the trial.

11. Confidence Intervals and Precision

The precision of a comparison depends on both its estimated value and the range of values compatible with the data under the analysis. For OCA 10 mg versus placebo, the recalculated risk difference is 0.012, with a 95% confidence interval from -0.036 to 0.061. For the titrated OCA regimen versus placebo, the estimate is 0.020, with a 95% confidence interval from -0.029 to 0.069. Each interval spans zero, so each includes no difference as one value compatible with the data.

The endpoints of those intervals also include differences in both directions. This means the estimates do not precisely determine whether the responder frequency was higher or lower relative to placebo in the underlying comparison. The point estimates alone are not sufficient to convey this uncertainty. The intervals are important because they show that the observed positive estimates should not be treated as exact or as proof of a positive difference.

The sponsor-reported response-ratio intervals likewise span the value 1: 0.71 to 1.79 for OCA 10 mg and 0.77 to 1.89 for the titrated regimen. On the ratio scale, 1 represents equal response frequencies. The intervals cover a broad range around that reference value. Because the sponsor’s estimates are response ratios and the recalculated estimates are risk differences, the numerical endpoints of their intervals are on different scales and should not be compared as if they measured the same quantity.

In general, confidence intervals express uncertainty under the method used; they do not incorporate every possible source of uncertainty. In particular, they do not resolve questions about missing biopsy information, the endpoint’s operational definition, or unreported analysis choices. The registry record does not report additional sensitivity analyses that would show how the estimates change under alternative assumptions. The intervals should therefore be read as statistical precision for the stated comparisons, not as a complete account of all uncertainty about the study.

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. Since the primary endpoint is a binary participant response, the figures are participants per arm. The time-to-event convention about total event counts does not apply to this outcome. The registry record does not report the trial’s own original sample-size assumptions, so the illustrations should not be mistaken for the enrollment target or the assumptions used to plan this study.

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 set to the stated fraction of the observed effect. The entries for 80% and 90% power describe the participants per arm that the calculation estimates would be needed to have the corresponding probability of detecting the assumed effect under those assumptions, if the effect and statistical model were as specified. They are not observed power.

The rows expressing 100% of the observed effect use the full observed estimate as the target for the illustration. Rows using 75% or 50% of the observed effect examine smaller target effects. Smaller effects are harder to distinguish from random variation, so the planning calculations require more participants per arm as the assumed effect becomes smaller. The plotted curve should be read as the same planning relationship across assumptions, not as a forecast of the actual study’s results.

These calculations are hypothetical design aids. They are particularly sensitive to the observed effect used as their starting point, which is itself uncertain. A sample-size figure derived from a noisy estimate does not guarantee that a later study will reproduce that effect or achieve the stated power. It also does not provide evidence that the completed trial was adequately or inadequately powered under its original plan. The original design assumptions and justification are not reported in the registry record.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.099; treatment proportion p₁ = 0.111; average p̄ = 0.105.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4340 = 0.8506.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4339 = 0.3652.
4. n = (0.8506 + 0.3652)² / (0.0124)² = 9,544.9, rounded up to 9,545 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 <- 0.0990415335463259                          # control proportion
p1 <- 0.111486486486486                          # 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(3439254)
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 = 9,545 (80% power), 12,778 (90% power)
 75% of observed effect: n per arm = 16,748 (80% power), 22,421 (90% power)
 50% of observed effect: n per arm = 37,184 (80% power), 49,778 (90% power)
power.prop.test: 9544.9 
Simulated power at n = 9,545 per arm: 0.800 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s reported primary analyses use Cochran-Mantel-Haenszel response ratios. For OCA 10 mg versus placebo, the registry reports a response ratio of 1.13, a 95% confidence interval from 0.71 to 1.79, and p = 0.617. For OCA 10 mg titrated to OCA 25 mg versus placebo, it reports a response ratio of 1.20, a 95% confidence interval from 0.77 to 1.89, and p = 0.418.

The recalculated comparisons instead use unadjusted risk differences from the posted responder counts and arm denominators. Their estimates are 0.012 and 0.020, with unadjusted p-values of 0.617 and 0.416, respectively. A response ratio expresses a relative contrast; a risk difference expresses an absolute contrast. The estimates and interval limits are consequently on different scales. The reported p-values are also not identical, because the registry analysis and simple re-calculation are not the same procedure.

The registry does not flag a discrepancy between the sponsor’s analysis and the re-calculation. The sponsor’s results should be treated as the registry’s own analysis, while the simple re-calculations provide a transparent, unadjusted comparison based on the posted summaries. Neither set of estimates should be treated as a replacement for the other, and the unadjusted calculations should not be described as an adjusted or stratified analysis. Both sets of intervals include their respective no-difference reference values, and both express uncertainty around the group contrast.

The record does not report enough methodological detail to reproduce the Cochran-Mantel-Haenszel implementation independently. Readers should therefore preserve the distinction between the sponsor-reported method and the recalculated summary-statistic comparison rather than assume that the calculations are interchangeable.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, comparisons, time points, or analysis populations. Each additional statistical test creates another opportunity for a chance finding. A prespecified testing hierarchy or adjustment can help control how the collection of tests is interpreted. The registry record lists multiple outcome measures and two reported primary comparisons against placebo, but does not report a multiplicity strategy, testing hierarchy, or adjustment for the results.

This absence does not demonstrate that the full trial protocol lacked such a strategy. It means the registry record does not document one in the information analyzed. Without the prespecified plan, it is not possible to determine from these entries whether particular outcomes or comparisons were designated as confirmatory, whether testing was sequential, or how the family of tests was intended to be handled. The unadjusted recalculations should not be treated as multiplicity-controlled results.

Missing data are also important for this endpoint because response requires an evaluable post-baseline biopsy. The responder definition excludes participants who died or discontinued treatment due to an adverse event, and requires biopsy assessment. The registry record does not report the number of participants without an evaluable biopsy, reasons for missing assessments, or further imputation or sensitivity-analysis methods. It therefore does not permit a full assessment of how missing assessments could affect the response estimates.

The record identifies the primary outcome population as ITT, but the posted definition also includes conditions that determine whether a participant qualifies as a responder. The available description does not provide enough detail to reconstruct the handling of every participant whose treatment, survival, or biopsy status did not satisfy the responder rule. That uncertainty should be kept distinct from the reported arm counts: the counts describe the result as posted, while missing-data methods and sensitivity analyses are not reported in the registry record.

Likewise, the registry record does not report an interim-analysis plan, stopping boundaries, or the trial’s original statistical analysis plan in sufficient detail to assess these issues. These are documentation limits, not evidence that a particular procedure was or was not used. Interpretations should stay within what the registry reports and avoid assuming unrecorded safeguards or analysis decisions.

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: bradycardia (3.9%), covid-19 pneumonia (3.4%), procedural pain (1.9%), covid-19 (1.4%), dyspnoea (1.4%).

During the double-blind phase, the registry reports serious adverse events for 43 participants among 312 at risk in the placebo group, 49 among 295 at risk in the OCA 10 mg group, and 46 among 309 at risk in the titrated OCA group. The recorded death counts are 4, 3, and 3, respectively. These are descriptive arm summaries. They should not be converted into causal conclusions from counts alone, particularly without further information about event timing, exposure, follow-up, and the analyses used.

The record also lists serious-event terms, including Bradycardia at 3.9%, COVID-19 pneumonia at 3.4%, Procedural pain at 1.9%, COVID-19 at 1.4%, Dyspnoea at 1.4%, and Hepatocellular carcinoma at 1.0%. The record excerpt does not specify the denominator or arm-specific distribution for these listed percentages, so they should be read as posted terms and percentages without assigning them to a particular group.

Serious adverse events and deaths are distinct summaries; a death count should not be assumed to be a subset of, or equivalent to, the serious-event count without further information. The registry record does not report enough detail to characterize event duration, severity grading beyond seriousness, attribution, or the statistical comparison of safety outcomes. These figures describe the posted safety record and do not by themselves establish a comparative safety profile.

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

The primary results describe the number of participants who met a specific biopsy-based responder definition during up to 18 months. The observed counts are 31.0 for placebo, 33.0 for OCA 10 mg, and 37.0 for OCA 10 mg titrated to OCA 25 mg. The recalculated risk differences are positive, but their confidence intervals include zero and extend to values in both directions. The sponsor-reported response-ratio intervals also include the no-difference reference value of 1.

These results do not establish a precise difference between either OCA regimen and placebo on the primary outcome. They also do not demonstrate that the groups are equivalent: an interval that includes no difference can still include potentially meaningful differences in either direction. Interpreting whether a range of effects is clinically important would require prespecified clinical thresholds and context that are not reported in the registry record.

The endpoint is not a direct measure of every aspect of NASH or cirrhosis. It requires improvement in fibrosis stage, no worsening in specified inflammation and ballooning grades, an evaluable post-baseline biopsy, and compliance with the treatment-discontinuation and survival conditions in the responder definition. The binary classification does not convey the degree of change for participants who responded, or the reason other participants did not satisfy the rule.

Results for baseline FIB-4 and ELF describe measurements before the treatment period and cannot be used to infer treatment-related change. The listed LSM change outcome has no numerical result reported in the registry record analyzed. The available safety counts are descriptive and do not, by themselves, establish comparative risks.

The findings should therefore be read as registry-recorded estimates with uncertainty, alongside limitations in documentation about missing data, multiplicity, and the original analysis plan. They are not medical advice and do not, on their own, settle how a treatment should be used. The registry data address a defined research question in a particular enrolled population, using a specific endpoint and follow-up period.

18. Why This Trial Matters Statistically

This trial is statistically informative because it pairs a randomized placebo comparison with a biopsy-based responder outcome in a population described as having compensated cirrhosis due to NASH. Randomization provides a framework for comparing assigned groups, while masking and the placebo comparator are design features intended to support interpretable group comparisons. The posted analysis nevertheless needs to be read through the endpoint definition, effect measure, and uncertainty intervals.

The primary endpoint illustrates why the point estimate is not the whole result. Both recalculated risk differences are positive, but their intervals include zero and cover values on either side of it. The sponsor’s response-ratio intervals also span the reference value of 1. A concise reading based only on the direction of the point estimates would omit the uncertainty that is central to interpreting the evidence.

The responder rule also makes the statistical outcome clinically specific but operationally complex. It requires a combination of fibrosis improvement, no worsening of named NASH features, survival, treatment continuation under the stated definition, and an evaluable biopsy. The resulting count is meaningful only in relation to those conditions. It cannot be generalized to every possible definition of histological improvement.

Finally, the record illustrates the importance of transparent analysis documentation. The sponsor-reported ratios and unadjusted risk-difference recalculations use different scales and methods. The registry record does not report the original design assumptions, multiplicity strategy, or further missing-data procedures. Those gaps limit the ability to evaluate the posted results against the complete planned analysis. Keeping observed estimates, precision, endpoint construction, and documentation limits distinct is essential to a careful statistical reading.

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 primary response requires an evaluable post-baseline biopsy, yet the registry record does not report the number of participants lacking one, the reasons for missing biopsies, or sensitivity analyses for missing outcome data. Because biopsy availability is part of the responder definition, these omissions limit assessment of how missing assessments relate to the posted responder counts. The record identifies the ITT Population but does not provide further details about the analysis handling of every participant who did not meet the operational response conditions.

The endpoint combines fibrosis improvement with no worsening in specified NASH components and conditions concerning discontinuation, death, and biopsy evaluation. This composite rule means the counts do not separately reveal the pattern of fibrosis change, inflammation, or ballooning. The registry record does not report component-level primary results in the information analyzed.

The posted sponsor analyses and simple recalculations use different measures and approaches: Mantel-Haenszel response ratios versus unadjusted risk differences. The registry record does not provide enough implementation detail to reproduce the sponsor analysis fully. The recalculations are consequently useful as transparent summaries from posted counts, but do not replace the registry’s own analysis or establish an adjusted treatment contrast.

The record does not report the original sample-size justification, full analysis plan, multiplicity approach, or additional sensitivity analyses. Although planning illustrations are available based on observed effects, they do not establish what assumptions guided the completed trial. Baseline FIB-4 and ELF do not measure treatment-period change, and numerical LSM change results are not reported in the record analyzed. Safety summaries are also descriptive; further information about attribution, timing, and analysis is not reported.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study Evaluating the Efficacy and Safety of Obeticholic Acid in Subjects With Compensated Cirrhosis Due to Nonalcoholic Steatohepatitis — NCT03439254.
• Registry record last updated 2023-10-23; status last verified 2023-10.
• Results first posted 2023-10-23.
• 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

NCT03439254 was a completed phase 3 randomized, quadruple-masked, placebo-controlled, multicenter, parallel-group study sponsored by Intercept Pharmaceuticals. It enrolled 919 participants with compensated cirrhosis due to NASH. The primary outcome counted participants who met the registry’s definition of improvement in fibrosis by at least 1 stage without worsening of specified NASH features, subject to survival, treatment-discontinuation, and biopsy-evaluation conditions.

Primary responder counts were 31.0 among 313.0 in the placebo group, 33.0 among 296.0 in the OCA 10 mg group, and 37.0 among 310.0 in the titrated OCA group. Recalculated risk-difference confidence intervals included zero for both comparisons. The sponsor’s reported response-ratio intervals included 1. The registry record also reports baseline FIB-4 and ELF summaries, serious adverse event counts, and deaths. Original design assumptions, multiplicity methods, and further missing-data procedures are not reported in the registry record.