A Study of Efruxifermin in Non-Cirrhotic Subjects With Histologically Confirmed Nonalcoholic Steatohepatitis (NASH): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Efruxifermin in Non-Cirrhotic Subjects With Histologically Confirmed Nonalcoholic Steatohepatitis (NASH) (NCT04767529), a randomized phase 2 study. The primary outcome is Effect of Efruxifermin (EFX) vs Placebo on Fibrosis Regression in Participants With Metabolic Dysfunction-associated Steatohepatitis (MASH)-Associated Stage 2 or 3 Fibrosis (F2 or F3).

2. Clinical Question

The endpoint combines a change in fibrosis stage with a condition on steatohepatitis. A participant qualifies only if fibrosis improves by at least one stage and the NASH Activity Score does not increase. Thus, an improvement in fibrosis alone does not meet the endpoint if the activity score worsens. The registry describes the fibrosis score as ranging from 0 to 4, with higher scores indicating greater fibrosis severity, and the activity score as ranging from 0 to 8.

This is a histology-based question in a defined non-cirrhotic population, rather than a question about symptoms, clinical events, or long-term outcomes. The result concerns the proportion meeting the stated biopsy endpoint at the specified assessment time. It does not, by itself, answer whether changes persist, affect other outcomes, or apply to people outside the studied population.

3. Trial Design

The registry identifies this as a Phase 2b, randomized, double-blind, placebo-controlled, parallel-group study, with quadruple masking recorded. It describes a multi-center evaluation of efruxifermin in non-cirrhotic participants with biopsy-proven F2-F3 NASH. The listed enrollment is 128, and the record status is completed. The study start is recorded as 2021-02-16 and primary completion as 2024-05-02.

There were three arms: placebo, efruxifermin 28 mg, and efruxifermin 50 mg. Each arm description specifies a once-weekly subcutaneous injection under double-blind conditions. The registry’s primary endpoint is measured at Week 24, and the primary analysis population is named the Week 24 Liver Biopsy Analysis Set. The arm denominators in that endpoint are 41 for placebo, 38 for the 28 mg dose, and 34 for the 50 mg dose. These are the denominators reported for that analysis, not the overall enrollment figure.

Randomization is intended to support a fair comparison by allocating participants to study arms through chance, while masking is intended to limit the influence of treatment knowledge on conduct and assessment. The registry labels the study quadruple-masked and describes the arms as double-blind; it does not identify which roles were included in the masking label. The allocation ratio and detailed randomization procedures are not reported in the registry record.

The study also lists secondary outcomes at Week 24 and Week 96, including histology measures and changes in hepatic fat fraction, lipoproteins, hemoglobin A1c, C-peptide, and adiponectin. The registry record lists 15 secondary outcomes and 16 outcome measures overall. Detailed findings are not available in the registry record for every listed secondary outcome, so their names should not be mistaken for evidence that a particular result occurred.

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: Week 24 Liver Biopsy Analysis Set

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: Randomly assigned to groups

6. Primary Endpoint

The registry lists the primary outcome as Effect of Efruxifermin (EFX) vs Placebo on Fibrosis Regression in Participants With Metabolic Dysfunction-associated Steatohepatitis (MASH)-Associated Stage 2 or 3 Fibrosis (F2 or F3), measured over 24 Weeks.

The primary endpoint is the proportion of participants with a biopsy-defined improvement in liver fibrosis of at least one stage and no worsening of steatohepatitis at Week 24. Fibrosis is graded using the NASH Clinical Research Network fibrosis score, described in the registry as ranging from 0 to 4 and increasing with severity. Steatohepatitis activity is assessed using the NASH Activity Score, ranging from 0 to 8 and combining steatosis, lobular inflammation, and hepatocyte ballooning.

This composite definition requires both parts to be satisfied. It is not simply a measure of fibrosis change, nor does it count improvement in one component if the other worsens. The endpoint therefore captures a specific histological response while retaining a safeguard against worsening in the activity score. The registry reports the outcome as participant counts in the Week 24 Liver Biopsy Analysis Set.

Biopsy-based endpoints are used to assess tissue-level changes that may not be captured by symptoms or routine clinical events over a study’s observation period. They also depend on biopsy assessment and the endpoint’s scoring rules. The registry record does not report further details about reading procedures, central review, or how missing biopsy results were handled. A result on this endpoint should be interpreted as evidence about the defined Week 24 histological measure, not as a direct measure of every aspect of health or subsequent clinical outcomes.

7. Results Posted in the Registry

• Efruxifermin 28 mg: 39.5% (15/38) versus 19.5% (8/41) on control; risk difference 20.0 percentage points (95% CI 0.2 to 39.7), risk ratio 2.02 (0.97–4.22); unadjusted two-proportion z-test p = 0.051.
• Efruxifermin 50 mg: 41.2% (14/34) versus 19.5% (8/41) on control; risk difference 21.7 percentage points (95% CI 1.2 to 42.2), risk ratio 2.11 (1.01–4.42); unadjusted two-proportion z-test p = 0.040.

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.

Proportion of Subjects Who Achieve Improvement in Liver Fibrosis ≥ 1 Stage and no Worsening of Steatohepatitis at Week 96

• 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:
  • Efruxifermin 28 mg: 46.2% (12/26) versus 23.5% (8/34) on control; risk difference 22.6 percentage points (95% CI -1.3 to 46.5), risk ratio 1.96 (0.94–4.09); unadjusted two-proportion z-test p = 0.065.
  • Efruxifermin 50 mg: 75.0% (21/28) versus 23.5% (8/34) on control; risk difference 51.5 percentage points (95% CI 30.0 to 72.9), risk ratio 3.19 (1.68–6.06); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Efruxifermin 28 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Efruxifermin 50 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes covering histology at Week 24 and Week 96, along with changes in hepatic fat fraction, lipoproteins, hemoglobin A1c, C-peptide, and adiponectin. The record lists 15 secondary outcomes, but the available detailed secondary results in the registry entries concern the Week 96 fibrosis-improvement endpoint. The endpoint descriptions alone do not establish the direction or size of findings for the other outcomes.

For the Week 96 fibrosis endpoint, the sponsor-reported pattern is more conclusive for the 50 mg comparison than for the 28 mg comparison: the reported interval for 28 mg spans zero and its reported p-value is 0.070, while the 50 mg analysis has a positive reported difference and p < 0.001. This is broadly consistent with the primary endpoint in the sense that the sponsor reports positive differences for both doses at Week 24, while the Week 96 evidence is not equally strong across dose comparisons. These results concern different assessment times and analyzed populations, and they should not be treated as interchangeable replications.

Secondary findings carry less weight when many outcomes are assessed, particularly when the registry record does not report whether multiplicity was controlled, which analyses were prespecified, or whether a testing hierarchy was used. A nominal p-value for a secondary comparison does not by itself establish confirmatory evidence. Secondary outcomes can help describe the breadth and consistency of the results, but they should be interpreted with the primary endpoint, uncertainty, analysis populations, and missing-data limitations in view.

No overall pattern can be established for every secondary outcome from the listed endpoint names. The registry record does not report detailed results for all the secondary measures in the registry record, so conclusions about those measures would go beyond the posted information.

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

• Proportion of Subjects Who Achieve Improvement in Liver Fibrosis ≥ 1 Stage and no Worsening of Steatohepatitis at Week 96
• Proportion of Subjects Who Achieve Resolution of Steatohepatitis and no Worsening of Liver Fibrosis at Week 24 and Week 96
• Proportion of Subjects Who Achieve Improvement in Liver Fibrosis ≥ 1 Stage at Week 24 and Week 96
• Change From Baseline in Hepatic Fat Fraction in EFX vs Placebo Groups
• Change From Baseline in Lipoproteins at Week 24 and Week 96
• Change From Baseline of Hemoglobin A1c (Glycated Hemoglobin, HbA1c) at Week 24 and Week 96
• Change From Baseline in C-peptide at Week 24 and Week 96
• Change From Baseline in Adiponectin at Week 24 and Week 96

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either meets the combined histological endpoint or does not. The registry therefore reports counts of participants meeting the endpoint and denominators in each arm. A binary outcome can be summarized as a proportion within each group and compared across groups using measures such as a risk difference, risk ratio, or odds ratio. These measures answer related but different questions, so estimates should be interpreted on the scale stated for the analysis.

What does a risk difference express?

A risk difference compares the proportions with the outcome in two groups by subtracting one proportion from the other. A positive risk difference means the observed proportion was higher in the efruxifermin group than in placebo. The simple recalculations are unadjusted comparisons based on the posted arm summaries. They do not incorporate information beyond those summaries. Their role is to provide a straightforward check, not to reconstruct every feature of the trial’s own analysis.

The sponsor’s reported measure is a percent difference, with estimates of 22.6 for 28 mg and 22.5 for 50 mg. The reported method is Cochran-Mantel-Haenszel. In general, this method can estimate an association between treatment group and a categorical outcome while accounting for strata. The registry record does not identify the stratification factors or give enough detail to reproduce the sponsor’s procedure. The reported estimates should therefore be described as the sponsor’s analysis, rather than treated as interchangeable with the unadjusted risk-difference recalculations.

What does a p-value say?

A p-value describes how compatible the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, nor is it a measure of the size or clinical importance of an effect. A smaller p-value indicates greater incompatibility with that null model, but does not remove uncertainty about the estimate or address limitations in the data and analysis.

The sponsor-reported p-values are 0.025 for the comparison of 28 mg with placebo and 0.036 for the comparison of 50 mg with placebo. The simple unadjusted recalculation gives p = 0.051 and p = 0.04, respectively. The difference between these values is a reminder that the method and analysis details matter. Because the record flags a discrepancy, the sponsor analysis is the primary reference for the trial’s reported inferential results; the recalculation is a separate, unadjusted check.

Why use a confidence interval?

A confidence interval gives a range of values compatible with the data and the analysis procedure at a stated confidence level. It conveys the estimate’s precision as well as its direction. A narrow interval indicates greater precision than a wide interval, while an interval spanning values on both sides of no difference can be consistent with a range of conclusions about direction. Confidence intervals are not guarantees that the true value lies in the particular interval, and they do not represent the range of individual participant responses.

The sponsor reports 95% confidence intervals for both primary comparisons. For 28 mg, the interval is 3.8 to 41.4 percentage points; for 50 mg, it is 1.6 to 43.3 percentage points. The intervals communicate substantial uncertainty about the magnitude of the percent difference, even though the sponsor’s reported analyses are labeled superiority. They should be read alongside the point estimates and p-values rather than as a substitute for either.

What does the analysis population represent?

The primary population is named the Week 24 Liver Biopsy Analysis Set. That tells the reader which analysis set the registry associates with the primary outcome, but the record does not define inclusion rules for that set in the registry entries. In particular, the registry record does not report the primary analysis population’s full specification, the handling of missing biopsies, or whether participants were analyzed according to randomized assignment. Those details are relevant because the outcome requires biopsy information.

The registry also reports arm-level denominators, which make clear that the outcome summaries apply to the participants represented in those analyses. They should not be confused with the study’s overall enrollment. Without the missing-data rules and population definition, it is not possible to assess from the posted information how exclusions or unavailable assessments may have influenced the estimates.

How should secondary analyses be treated?

Secondary outcomes can add context by examining other time points, histological measures, or laboratory measures. They do not automatically have the same evidential status as the primary endpoint. When many outcomes or comparisons are tested, the chance of obtaining a nominally unusual result by chance can increase. Adjustments or a prespecified hierarchy can address some multiplicity concerns, but the registry record does not report a multiplicity procedure or a hierarchy for interpreting secondary outcomes. General statistical practice is therefore to treat unadjusted secondary findings as exploratory or supportive, not as independent confirmation of a primary finding.

The record reports the Cochran-Mantel-Haenszel method for the primary comparisons and lists outcome analyses, but the broader statistical analysis plan is not reported in the registry record. Details such as stratification factors, covariate adjustment, prespecification of each analysis, and any interim analyses are not reported in the registry record. They should not be inferred from the outcome summaries or from the name of the reported method.

11. Confidence Intervals and Precision

The sponsor’s primary estimates are accompanied by 95% confidence intervals. For the 28 mg comparison, the reported percent difference is 22.6 percentage points, with an interval from 3.8 to 41.4. For the 50 mg comparison, the estimate is 22.5 percentage points, with an interval from 1.6 to 43.3. Both intervals are broad relative to their point estimates, so the exact magnitude of the difference is uncertain. The intervals are compatible with a range of positive differences rather than identifying one precise effect size.

Both sponsor-reported intervals lie above zero, consistent with the positive differences and the reported p-values. This describes the results under the sponsor’s analysis; it does not mean the size of the effect is known precisely or that the same estimate would necessarily be observed in another study. Confidence intervals reflect sampling uncertainty under the analysis assumptions and do not account for every possible source of bias, measurement error, or missing outcome data.

The recalculated comparisons have their own intervals, based on unadjusted calculations from the posted arm summaries. They are not the same estimand and method as the sponsor’s Cochran-Mantel-Haenszel analyses. The discrepancy between the recalculated and reported analyses is therefore relevant to how the results are presented. The registry record does not provide enough detail to reconcile the methods or explain the difference. In keeping with that discrepancy, the sponsor analysis is the primary account of the trial’s reported result, while the recalculation serves as a separate check.

Precision is also limited by the number of participants represented in the Week 24 biopsy analysis, particularly when a binary outcome is based on relatively few participants meeting its definition. The posted counts and confidence intervals convey uncertainty more fully than a p-value alone. They do not show the distribution of individual biopsy changes, and no individual-level data are reported in the registry record.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning illustrations give the number of participants per arm for the binary outcome comparisons. They are not total event counts. The listed 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 original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the planned number of participants per arm that, under those assumptions, would give an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding planning target for a 90% chance. These are prospective planning calculations, not evidence about what the completed trial was capable of detecting after its results were known.

Planning scenarios are presented for the full observed effect and for smaller fractions of that effect. Smaller effects require more participants to detect with the same nominal power and significance level, which is why the planning figures rise as the effect to detect is reduced. These figures use the observed effect as a starting point, so they are illustrations rather than the basis of the study’s original design. They are not observed power. Observed power calculated from the effect estimate after a study is complete does not add a useful measure of evidence beyond the estimate, confidence interval, and test result.

The calculations assume equal allocation for the two arms being compared, but the registry record does not report that the original trial used equal allocation. The planning values also do not, in the assumptions listed, account for departures from those conditions or for missing outcome data. They should be read as conditional examples of how a hypothetical design might be sized, not as a report of the trial’s actual enrollment plan.

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 = 0.195; treatment proportion p₁ = 0.395; average p̄ = 0.295.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6449 = 1.2640.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6293 = 0.5296.
4. n = (1.2640 + 0.5296)² / (0.1996)² = 80.7, rounded up to 81 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 <- 0.195121951219512                          # control proportion
p1 <- 0.394736842105263                          # 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(4767529)
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 = 81 (80% power), 108 (90% power)
 75% of observed effect: n per arm = 137 (80% power), 183 (90% power)
 50% of observed effect: n per arm = 291 (80% power), 389 (90% power)
power.prop.test: 80.7 
Simulated power at n = 81 per arm: 0.805 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparisons using the Cochran-Mantel-Haenszel method. For 28 mg versus placebo, the sponsor reports a percent difference of 22.6, a 95% confidence interval from 3.8 to 41.4, and p = 0.025. For 50 mg versus placebo, the corresponding reported difference is 22.5, with a 95% confidence interval from 1.6 to 43.3 and p = 0.036. Both analyses are labeled as superiority analyses in the record.

The recalculations use only the posted group counts and denominators and produce unadjusted risk differences. Their p-values do not exactly match the sponsor-reported values. The registry record flags this discrepancy, so the sponsor’s own analysis takes precedence when stating the trial’s reported findings. The unadjusted calculations remain useful for understanding the crude comparison implied by the arm summaries, but they should not be presented as a correction to or replacement for the sponsor’s analysis.

The registry record does not provide sufficient detail to determine which methodological choices account for the difference. It would be inappropriate to attribute the discrepancy to particular adjustments, strata, or missing-data procedures without that information. The sponsor’s estimates and the simple recalculations should be kept distinct in interpretation, with the method and scale named for each.

15. Multiplicity, Missing Data and Analysis Populations

The study includes a primary endpoint and numerous secondary outcomes, with 40 analyses reported in the registry record. When multiple outcomes, time points, or treatment comparisons are examined, the probability of at least one apparently unusual result can increase even if there is no underlying effect. Statistical procedures such as adjustment for multiple testing or a prespecified hierarchy can help control this issue. The registry record does not report whether such a procedure was used, how the primary and secondary outcomes were ordered, or which results were intended to be confirmatory.

The sponsor’s primary analyses are reported as superiority analyses, but the record does not provide a complete statistical analysis plan. Interim analyses, stopping rules, planned covariate adjustment, and the rationale for the analysis populations are not reported in the registry record. The absence of these details does not show that the procedures were absent; it means they cannot be evaluated from the posted record.

Missing outcome data are especially relevant to the primary endpoint because it depends on a Week 24 liver biopsy. The registry names the Week 24 Liver Biopsy Analysis Set and reports denominators by arm, but does not describe how participants without an available biopsy were handled or what assumptions were used. It also does not report sensitivity analyses for missing biopsy outcomes. The record therefore does not establish whether the posted analysis accounts for all randomized participants or how robust the result is to alternative assumptions about missing data.

These gaps limit assessment of the risk of bias and the strength of confirmatory claims. They do not erase the sponsor-reported comparisons, but they make it important to distinguish the reported result from information not available in the registry record. The findings should be interpreted with attention to the analysis population, the endpoint’s biopsy requirement, and the unresolved multiplicity and missing-data details.

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: gastritis (2.5%), pancreatitis (2.5%), arteriospasm coronary (2.5%), ankle fracture (2.5%), lower limb fracture (2.5%).

The registry reports serious adverse event figures separately by arm. Serious adverse events affected 4 of 43 participants at risk in the placebo group, 4 of 40 in the 28 mg group, and 7 of 43 in the 50 mg group. The record reports zero deaths in each arm. These are descriptive counts and denominators; they do not by themselves establish whether an event was caused by study treatment.

Other adverse events affected 42 of 43 participants at risk in the placebo group, 38 of 40 in the 28 mg group, and 43 of 43 in the 50 mg group. The registry also lists serious-event terms, each with a reported frequency of 2.5%: gastritis, pancreatitis, coronary arteriospasm, ankle fracture, lower limb fracture, and panic attack. The record does not map these listed terms to particular arms in the registry record.

Adverse-event counts should be interpreted in light of the study’s size, observation period, definitions, and the way events were collected. The registry record does not provide enough detail to compare event severity or duration, exposure-adjusted rates, or causal attribution. These figures are a descriptive safety summary, not a standalone judgment about comparative safety.

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

The primary result addresses a narrowly defined question: the proportion of participants in the Week 24 biopsy analysis who met a combined fibrosis and steatohepatitis histology criterion. The sponsor’s reported analyses show positive differences in both efruxifermin groups compared with placebo, and both are labeled superiority analyses. The confidence intervals and p-values describe the uncertainty under that reported approach.

The result does not establish that every participant improved, or that the observed group-level difference applies to an individual. It does not address outcomes beyond the endpoint definition, nor does it establish how changes in biopsy scores relate to symptoms, long-term clinical events, or other outcomes. The registry record includes secondary endpoints, but detailed results for all listed outcomes are not available in the registry record.

The study enrolled non-cirrhotic participants with biopsy-proven F2-F3 NASH. Findings from this population should not automatically be extended to people with cirrhosis or to other populations not described in the record. The endpoint is assessed at Week 24, so it does not by itself establish durability. Although the record lists Week 96 outcomes, those are separate assessments and are subject to their own denominators and analysis uncertainty.

The primary inference also depends on the analysis method and population. The sponsor’s reported estimates differ from the simple unadjusted recalculations, and the registry flags a discrepancy. The sponsor’s own analysis therefore takes precedence as the trial’s reported result. Missing-biopsy handling, the complete analysis plan, and multiplicity procedures are not reported in the registry record, limiting how fully the analysis can be assessed.

Accordingly, the posted findings are evidence about a specific Week 24 histological outcome under the sponsor’s analysis, not a complete account of all potential benefits or harms. They do not justify medical advice or conclusions beyond the measured endpoint and study population.

18. Why This Trial Matters Statistically

This trial illustrates why a treatment comparison should be read through its endpoint definition, analysis population, and estimation method rather than through a single p-value. The primary outcome is a binary composite requiring both fibrosis improvement and no worsening of steatohepatitis. That definition determines which participants count as having the outcome and makes the result specific to a biopsy-based assessment at Week 24.

The record also illustrates the distinction between sponsor-reported inference and an unadjusted recalculation from arm summaries. Both are legitimate descriptions of different analyses, but they are not interchangeable. Because the record flags a discrepancy, the sponsor’s reported analysis is the principal account of the trial result. Keeping the recalculation separate avoids implying that a simple summary-based calculation reproduces the sponsor’s full method.

Confidence intervals add information that a threshold-based interpretation misses. They show the range of effect estimates compatible with the analysis and signal that the size of the difference remains uncertain. The result can be statistically supported under the sponsor’s reported method while still leaving substantial uncertainty about magnitude and applicability.

Finally, the study presents common challenges in interpreting a trial record: multiple secondary outcomes, a biopsy-dependent analysis population, and incomplete reporting of multiplicity and missing-data methods. These are not reasons to dismiss the posted results, but they are essential context for weighing how much the results establish. Careful statistical interpretation preserves both the evidence in the analysis and the limits of what the record documents.

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.

Several trial-specific limitations affect interpretation. The primary endpoint depends on a Week 24 liver biopsy, but the registry record does not report how missing or unevaluable biopsies were handled. It names the analysis set without providing its full inclusion rules. The reported denominators therefore describe the analyzed participants, but the record does not explain their relation to all randomized participants or the reasons for differences among the denominators.

The registry reports the sponsor’s Cochran-Mantel-Haenszel method but does not state the stratification factors or enough detail to reproduce the analysis. The sponsor’s results differ from unadjusted recalculations based on the posted counts. The record flags the discrepancy, and the sponsor analysis takes precedence, but the reason for the difference is not reported in the registry record.

There are many listed outcomes and analyses, while multiplicity control and any prespecified testing hierarchy are not reported in the registry record. This makes it difficult to distinguish confirmatory secondary evidence from exploratory findings. Detailed results for every secondary outcome are not available in the registry record, limiting assessment of consistency across outcomes.

The posted primary result is measured at Week 24 and is histological. It does not alone establish the persistence of the finding or its relation to clinical outcomes. The study population is non-cirrhotic participants with biopsy-proven F2-F3 NASH, so extrapolation beyond that population is not established by this record. The record’s adverse-event summary is also descriptive and does not provide enough information to establish causality or compare exposure-adjusted event rates.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Efruxifermin in Non-Cirrhotic Subjects With Histologically Confirmed Nonalcoholic Steatohepatitis (NASH) — NCT04767529.
• Registry record last updated 2025-06-18; status last verified 2025-06.
• Results first posted 2025-05-08.
• 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

The registry describes a completed Phase 2b randomized, double-blind, placebo-controlled, parallel-group study of efruxifermin in non-cirrhotic participants with biopsy-proven F2-F3 NASH. The listed enrollment is 128. Participants were assigned to placebo, efruxifermin 28 mg, or efruxifermin 50 mg, with once-weekly subcutaneous injections described for each arm.

The primary outcome was the proportion meeting a Week 24 biopsy definition of at least one-stage fibrosis improvement without worsening of steatohepatitis. The sponsor reported positive percent differences versus placebo for both doses using a Cochran-Mantel-Haenszel analysis. Simple unadjusted recalculations differ from those reported values; because the registry flags a discrepancy, the sponsor’s analysis takes precedence.

The record lists multiple secondary and safety outcomes, but does not report all details needed to assess multiplicity, missing biopsy data, or the complete analysis plan. Results should be interpreted as evidence about the specified histological endpoint and population, with those reporting limitations in view.