A Phase 2b Study of Icosabutate in Fatty Liver Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase 2b Study of Icosabutate in Fatty Liver Disease (NCT04052516), a randomized phase 2 study. The primary outcome is Percentage of Patients With Resolution of NASH, Defined as Disappearance of Ballooning (Score = 0) With Lobular Inflammation Score 0 or 1, With no Worsening of Fibrosis..

2. Clinical Question

3. Trial Design

This was a phase 2b, randomized, double-blind, placebo-controlled, parallel-group study of NST-4016 in patients with NASH. The intervention listings identify NST-4016 as icosabutate. The registry describes quadruple masking, randomized allocation, and a completed study. The sponsor is NorthSea Therapeutics B.V.

The registry reports enrollment of 280. The listed treatment groups were placebo, icosabutate 300mg, and icosabutate 600mg. The arm descriptions specify oral capsules taken once daily for 52 weeks for each group. The primary endpoint timeframe was 52 weeks, and the primary population was the 3-Panel Modified Intent-To-Treat population based on baseline and Week 52, or ET if applicable, liver biopsy reads and eligibility under the 3-panel read paradigm.

The recorded study start was 2019-07-17 and primary completion was 2022-02-20. Those dates describe the registry record and do not by themselves describe the timing of individual analyses or the duration of follow-up beyond the stated endpoint timeframe.

The registry lists 13 outcome measures and indicates that 12 secondary outcomes were posted. These include fibrosis improvement definitions, liver enzymes, bilirubin, inflammation and fibrosis markers, and insulin resistance. The results excerpt includes primary endpoint analyses and selected secondary outcome results; the remaining secondary outcome results are not reported in the registry record summarized in these data. Details of the original sample-size justification, the randomization procedure, allocation concealment, any interim analyses, and the full statistical analysis plan 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: 3-Panel Modified Intent-To-Treat (mITT) Population - The 3-Panel mITT Population included all patients who had a baseline and Week 52 (or ET, if applicable) liver biopsy read and fulfilled eligibility criteria based on the 3-panel read paradigm. This population was considered the primary population for the efficacy analysis of the histology data. Biopsy fibrosis score F2/F3

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: The Modified Intent-To-Treat (mITT) Population is used for the baseline analysis population as this was the primary population for efficacy analysis. The mITT Population included all patients from the ITT Population who had valid baseline and Week 52 (or ET, if applicable) liver biopsy measurements; a valid Week 52/ET liver biopsy was defined as a liver biopsy that had occurred within 90 days of last dose/Week 52 visit.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Patients With Resolution of NASH, Defined as Disappearance of Ballooning (Score = 0) With Lobular Inflammation Score 0 or 1, With no Worsening of Fibrosis., measured over 52 weeks.

The primary endpoint is the percentage of participants with NASH resolution at 52 weeks, defined as disappearance of ballooning (score = 0) alongside a lobular inflammation score of 0 or 1, with no worsening of fibrosis. It is a binary response outcome: each person in the defined analysis population either meets the endpoint criteria or does not. Reporting the percentage expresses how often the composite biopsy-based definition was met in each treatment group.

The endpoint combines features of steatohepatitis activity with a condition on fibrosis. That structure matters for interpretation: resolution under this definition requires improvement in the specified NASH features without a worsening in fibrosis. It is not interchangeable with the separate secondary measures of fibrosis improvement, which ask whether fibrosis stage improved under their own definitions.

Biopsy-based outcomes can operationalize tissue changes using prespecified scoring criteria, but the registry does not report information about biopsy-reader agreement or the detailed procedures used to resolve disagreement. The analysis population also depends on biopsy reads at baseline and Week 52, or ET if applicable, and fulfillment of eligibility criteria under the stated read paradigm. Therefore, the endpoint percentages describe that specified population and should not be read as outcomes for everyone enrolled. The original protocol rationale for choosing this endpoint and its relation to longer-term clinical outcomes are not reported in the registry record.

7. Results Posted in the Registry

• Icosabutate 300mg: 17.3% (9/52) versus 8.7% (4/46) on control; risk difference 8.6 percentage points (95% CI -4.5 to 21.7), risk ratio 1.99 (0.66–6.03); unadjusted two-proportion z-test p = 0.210.
• Icosabutate 600mg: 20.8% (11/53) versus 8.7% (4/46) on control; risk difference 12.1 percentage points (95% CI -1.6 to 25.7), risk ratio 2.39 (0.82–6.99); unadjusted two-proportion z-test p = 0.095.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percentage of Patients With Fibrosis Improvement, Defined as Greater Than or Equal to 1 Stage of Fibrosis Improvement and no Worsening of Steatohepatitis (Inflammation/Ballooning).

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Icosabutate 300mg: 26.9% (14/52) versus 13.0% (6/46) on control; risk difference 13.9 percentage points (95% CI -1.6 to 29.4), risk ratio 2.06 (0.86–4.93); unadjusted two-proportion z-test p = 0.089.
  • Icosabutate 600mg: 24.5% (13/53) versus 13.0% (6/46) on control; risk difference 11.5 percentage points (95% CI -3.6 to 26.6), risk ratio 1.88 (0.78–4.55); unadjusted two-proportion z-test p = 0.148.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Icosabutate 300mg 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 Icosabutate 600mg and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Patients With Fibrosis Improvement, Defined as Greater Than or Equal to 1 Stage of Fibrosis Improvement.

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Icosabutate 300mg: 30.8% (16/52) versus 13.0% (6/46) on control; risk difference 17.7 percentage points (95% CI 1.8 to 33.6), risk ratio 2.36 (1.01–5.52); unadjusted two-proportion z-test p = 0.036.
  • Icosabutate 600mg: 28.3% (15/53) versus 13.0% (6/46) on control; risk difference 15.3 percentage points (95% CI -0.3 to 30.8), risk ratio 2.17 (0.92–5.13); unadjusted two-proportion z-test p = 0.064.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Icosabutate 300mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Icosabutate 600mg and the control. The interval gives the range of effects that remain compatible with the data.

Change in Bilirubin Micromol/L From 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 errors.
• Result:
  • Icosabutate 300mg: mean -1.11 versus 0.56 on control; difference -1.67 (95% CI -2.63 to -0.71), standardized effect d = -0.63; z-test p = <0.001.
  • Icosabutate 600mg: mean -1.49 versus 0.56 on control; difference -2.05 (95% CI -2.96 to -1.14), standardized effect d = -0.78; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Icosabutate 300mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Icosabutate 600mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the posted secondary outcomes, the registry includes measures of fibrosis improvement, liver enzymes, bilirubin, inflammation and fibrosis activity markers, and insulin resistance. This range is useful for seeing whether the study examined related biological and tissue-level outcomes alongside the primary biopsy-based NASH resolution definition. The available results are not a single unified endpoint, and each measure has its own definition, scale, analysis population, and precision.

The secondary fibrosis outcomes concern improvement in fibrosis stage, with one definition additionally requiring no worsening of steatohepatitis. These questions are related to the primary endpoint because fibrosis is part of its no-worsening condition, but they are not the same outcome: the primary endpoint requires a specified pattern of NASH resolution, whereas the secondary endpoints focus on fibrosis improvement. The enzyme, bilirubin, marker, and insulin-resistance outcomes address other dimensions and cannot substitute for the primary response definition.

Secondary findings should generally carry less weight than a prespecified primary result when many outcomes and comparisons are examined. Repeated testing increases the chance of observing an apparently notable result by chance unless multiplicity is addressed. The registry record does not report a multiplicity adjustment or enough information to establish which secondary comparisons were prespecified for confirmatory interpretation. Their results are best treated as exploratory or supportive descriptions rather than as independent proof of a treatment effect.

The listed outcome measure count is 13, and 12 secondary outcomes are indicated as posted. Not all listed secondary results are included in the available outcome detail; absent results are not reported in the registry record. A complete assessment of consistency across every planned secondary measure is therefore not possible from the record. In general, the secondary outcomes can add context and generate hypotheses, but they do not override the uncertainty in the primary analysis.

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

• Percentage of Patients With Fibrosis Improvement, Defined as Greater Than or Equal to 1 Stage of Fibrosis Improvement and no Worsening of Steatohepatitis (Inflammation/Ballooning).
• Percentage of Patients With Fibrosis Improvement, Defined as Greater Than or Equal to 1 Stage of Fibrosis Improvement.
• Changes in the Liver Enzymes Aspartate Aminotransferase (AST)U/L, Alanine Aminotransferase ( ALT)U/L and Gamma Glutamyl Transferase (GGT) U/L From Baseline
• Change in Bilirubin Micromol/L From Baseline
• Change From Baseline in Inflammation Marker hsCRP
• Change From Baseline in Fibrosis Activity Marker Pro-C3
• Change From Baseline in Fibrosis Activity Marker Enhanced Liver Fibrosis (ELF) Test
• Change From Baseline in Homeostasis Model Assessment of Insulin Resistance (HOMA-IR)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary, expressed as the percentage of participants meeting the endpoint definition. For this type of outcome, the observed proportion is the number meeting the response criteria relative to the number assessed in that group. The registry’s primary population is the 3-Panel Modified Intent-To-Treat population, defined using biopsy reads and eligibility criteria. Its group sizes for the primary outcome are not necessarily the same as the overall enrollment or safety populations.

What does a risk difference describe?

A risk difference compares the response proportion in one group with the response proportion in another. A value of zero represents equal observed proportions; a positive value means the proportion is higher in the intervention group for the contrast as oriented. The recalculated risk differences use posted group summary counts and are unadjusted. They are useful as a direct scale for comparing absolute response proportions, but they do not reproduce the sponsor’s Cochran-Mantel-Haenszel analysis.

The recalculated risk ratios and odds ratios are other ways to express binary comparisons. A risk ratio compares proportions as a ratio, while an odds ratio compares the odds of response. These scales are not interchangeable, particularly when response proportions are not very small. The sponsor reported odds ratios using a Cochran-Mantel-Haenszel method. That method combines information across strata; the identities and handling of the strata are not reported in the registry record. Consequently, the sponsor’s reported odds ratios and the unadjusted recalculated risk differences answer closely related but not identical statistical questions.

How should a p-value be read?

A p-value describes how incompatible 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, and it does not measure the size or clinical importance of an effect. The recalculated p-values are explicitly unadjusted comparisons. The registry’s reported p-values come from the sponsor’s analyses. Neither should be interpreted without the corresponding estimate, interval, analysis population, and method.

For binary outcomes, relatively few response events can make estimates unstable and intervals wide. A small change in observed counts can materially affect the estimated difference. That general statistical consideration is relevant to interpreting the primary endpoint, whose posted group response counts are limited. It does not establish that any particular analysis is biased; it explains why precision must be considered alongside the point estimates.

What does the confidence interval add?

A confidence interval gives a range of estimates compatible with the observed data under the method’s assumptions. It conveys uncertainty in a way that a point estimate alone cannot. An interval that includes the null value does not prove the groups are equivalent; it indicates that the data do not precisely distinguish the estimated contrast from the null at the interval’s stated confidence level. The interval also shows which materially different effects remain compatible with the data.

The sponsor’s reported primary results are odds ratios with 95% confidence intervals. The recalculated comparisons are risk differences with intervals. Since the measures use different scales and methods, their numerical values should not be compared as though they were identical quantities. Both sets of results indicate uncertainty that warrants restraint in conclusions.

Why distinguish analysis populations?

Randomized allocation describes how participants were assigned, but an outcome analysis may use a defined subset based on endpoint availability and eligibility. Here, the primary population requires biopsy information at baseline and Week 52, or ET if applicable, and eligibility under the 3-panel read paradigm. The registry does not provide the full participant flow or explain all reasons for missing biopsy results. If endpoint availability is related to treatment response or participant characteristics, a complete-case endpoint analysis may differ from an analysis of all randomized participants. The direction and magnitude of any such effect cannot be determined from the record.

Continuous secondary outcomes use a different framework. For bilirubin, the registry reports least-squares mean changes with standard errors, and the recalculated comparison is a mean difference. A mean summarizes the central value on a continuous scale; its standard error describes the uncertainty in estimating that mean. The posted recalculation derives an approximate standard deviation from the reported standard errors and sample sizes, as indicated in the analysis details. It is therefore an unadjusted re-calculation, not the sponsor’s model-based comparison. General statistical caution applies: a continuous measure and a binary response endpoint describe different outcome properties and should not be treated as interchangeable evidence.

The registry does not report the full model specifications, covariates, missing-data methods, multiplicity procedure, or original sample-size assumptions. These omissions prevent a complete independent reconstruction of the sponsor’s inferential framework. The posted summary statistics support transparent descriptive comparisons, but they cannot resolve every design and analysis question.

11. Confidence Intervals and Precision

Precision is about how tightly an estimate is determined by the data. The primary response percentages are point estimates, while their confidence intervals describe uncertainty around comparisons between groups. In the unadjusted recalculations, the risk-difference interval for icosabutate 300mg versus placebo runs from -0.045 to 0.217, and the interval for icosabutate 600mg versus placebo runs from -0.016 to 0.257. Each includes zero, the value representing no difference in response proportions.

The breadth of these intervals means that the data remain compatible with a range of possible differences. They include values on both sides of zero, so they do not precisely establish the direction of the underlying difference. The corresponding recalculated p-values are 0.21 and 0.095. A p-value is not a measure of precision by itself; the estimates and intervals are more informative about the range of effects consistent with the analysis.

The sponsor’s 95% confidence intervals are reported on the odds-ratio scale: 0.62 to 4.63 for icosabutate 300mg versus placebo and 0.80 to 5.08 for icosabutate 600mg versus placebo. For odds ratios, the null value is 1, and both intervals include it. Their widths also indicate substantial uncertainty about the magnitude of the odds ratios.

These intervals arise from different statistical methods and effect scales, so they should be read separately rather than treated as duplicate calculations. The registry does not report a protocol-based precision target or the original assumptions used to design the trial. The observed uncertainty therefore cannot be judged against a documented design goal 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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design calculations. They assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is the stated fraction of the observed effect. For these non-time-to-event outcomes, the figures are participants per arm; the rule for time-to-event outcomes would be a total number of events, but the primary endpoint is not time-to-event.

The 80% power column gives the planned participants per arm for an illustrative design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the assumptions were true. The 90% power column gives the corresponding per-arm figure for a design targeting 90% power. Higher target power generally requires more participants for the same assumed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

Rows for planning for 100% of the observed effect use the observed comparison as the target effect; rows for planning for 75% or 50% use smaller target effects. Smaller effects are harder to distinguish from random variation, so they require more participants under the same planning framework. These figures are not observed power: observed power is not an appropriate retrospective measure of whether the trial “had enough” participants, and these calculations instead illustrate prospective sample sizes under specified assumptions.

The displayed values are not a recommendation or a reconstruction of the trial’s actual design. They depend on the observed effect, which is uncertain, and may not reflect clinically meaningful target differences or the analysis plan that governed the study. The registry record does not report whether the original study used these assumptions or a different planning method.

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 = 0.087; treatment proportion p₁ = 0.173; average p̄ = 0.130.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4756 = 0.9322.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4717 = 0.3970.
4. n = (0.9322 + 0.3970)² / (0.0861)² = 238.2, rounded up to 239 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 <- 0.0869565217391304                          # control proportion
p1 <- 0.173076923076923                          # 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(4052516)
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 = 239 (80% power), 319 (90% power)
 75% of observed effect: n per arm = 395 (80% power), 527 (90% power)
 50% of observed effect: n per arm = 818 (80% power), 1,095 (90% power)
power.prop.test: 238.2 
Simulated power at n = 239 per arm: 0.809 (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 analyses as Cochran-Mantel-Haenszel odds ratios. The reported estimate for icosabutate 300mg versus placebo is 1.70, with a 95% confidence interval from 0.62 to 4.63 and p = 0.299. For icosabutate 600mg versus placebo, the reported estimate is 2.01, with a 95% confidence interval from 0.80 to 5.08 and p = 0.139.

The recalculated results use unadjusted comparisons of posted summary counts and report risk differences, with their own intervals and p-values. They are not a reproduction of the sponsor’s Cochran-Mantel-Haenszel analysis. The reported odds ratios and the recalculated risk differences use different effect scales, and the sponsor method may incorporate strata whose details are not reported in the registry record. Accordingly, a difference in numerical estimates or p-values should not automatically be treated as a contradiction.

The record marks no discrepancy between the posted results and the recalculation. The sponsor analysis is therefore presented as the registry-reported inferential analysis, while the recalculation is an additional, simple unadjusted comparison from summary statistics. Neither set of results removes the uncertainty reflected in its confidence intervals. The registry does not provide enough detail to reconstruct the sponsor’s complete model or assess every feature of its implementation.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, doses, or group comparisons. Even when each individual statistical test uses a conventional threshold, conducting many tests increases the chance that at least one result appears notable by chance. Statistical approaches to address multiplicity can include prespecifying a testing order, adjusting significance thresholds, or controlling an error rate across a family of hypotheses. The registry record does not report whether any such procedure was planned or used for the primary and secondary outcomes.

The primary endpoint compares placebo with two icosabutate dose groups, and the registry lists multiple secondary outcomes. This creates more than one inferential question. The unadjusted recalculated p-values should therefore be read as unadjusted, not as multiplicity-controlled evidence. The sponsor’s reported primary p-values are listed, but the complete analysis plan and any multiplicity strategy are not reported in the registry record. It cannot be assumed that a particular correction was or was not prespecified.

Missing outcome information also matters. The primary analysis population requires a baseline and Week 52, or ET if applicable, biopsy read and eligibility under the specified paradigm. The registry does not report complete participant flow, the reasons participants lacked endpoint data, or the missing-data assumptions and methods. It is therefore not possible to determine from the posted results whether missing endpoint information could have affected the estimated response percentages or in which direction.

The registry does not report whether interim analyses took place, whether stopping rules were specified, or the original sample-size justification. The listed primary population is not identical by definition to everyone enrolled, and the safety counts use a different group of participants at risk. These distinctions are important when comparing efficacy and safety results; denominators should not be assumed to be the same across outcomes.

These are reporting limitations, not evidence that a particular procedure was absent or that the analyses were improperly conducted. Without the prespecified plan and fuller participant-level accounting, readers cannot fully evaluate outcome selection, missingness handling, or the control of false-positive findings across all comparisons.

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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cellulitis (2.1%), coronavirus infection (1.1%), transient ischemic attack (1.1%), post-procedural hematoma (1.1%), bladder transitional cell carcinoma (1.1%).

The registry reports serious adverse event counts and the numbers at risk by group. Serious adverse events affected 4 participants in the placebo group, 5 in the icosabutate 300mg group, and 8 in the icosabutate 600mg group. The corresponding numbers at risk are 91, 92, and 95. Deaths are reported as 1, 0, and 1, respectively. These counts describe the safety information posted in the registry; they do not establish that an event was caused by a study treatment.

The record also reports other adverse events affecting 82 participants in the placebo group, 80 in the icosabutate 300mg group, and 80 in the icosabutate 600mg group, with 91, 92, and 95 at risk, respectively. The serious-event terms listed include cellulitis at 2.1%, and coronavirus infection, transient ischemic attack, post-procedural hematoma, bladder transitional cell carcinoma, and abdominal pain at 1.1% each. Those terms and percentages should be read as registry-reported event listings, not as evidence of comparative risk or causation.

Safety denominators differ from the primary endpoint analysis population, so these counts should not be compared directly with efficacy group sizes. The registry record does not provide event timing, severity grading beyond serious status, treatment-relatedness judgments, exposure-adjusted rates, or detailed definitions for every reported category. The counts alone cannot establish whether safety profiles differ, particularly without fuller context about follow-up and adjudication.

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

The primary result describes the percentage meeting a specific biopsy-based definition of NASH resolution without worsening of fibrosis at 52 weeks in the stated 3-Panel Modified Intent-To-Treat population. The posted percentages are higher in both icosabutate groups than in placebo. This is a descriptive pattern in the trial data, not by itself a definitive estimate of what would occur in other populations or over other timeframes.

The recalculated risk-difference intervals include zero, and the sponsor’s reported odds-ratio intervals include 1. Both analyses therefore retain uncertainty about whether the underlying group contrast differs from the null. This does not demonstrate that the groups are equivalent, and it does not prove there is no effect. Rather, the available estimates are not precise enough to rule out a range of possible contrasts.

The endpoint is a response definition based on biopsy features, not a measure of every clinical consequence of NASH. The registry does not report long-term outcomes or establish whether the endpoint changes translate into outcomes that matter to patients. Nor does a result at 52 weeks establish durability beyond that timeframe.

Interpretation also depends on the defined analysis population, the completeness of biopsy follow-up, and the statistical approach. The record does not provide full missing-data methods, the original analysis plan, or multiplicity handling. It also reports several secondary outcomes, which should not be treated as independent confirmation without knowing how they were selected and analyzed.

Accordingly, the data support a careful statement about observed group percentages and uncertainty, not a treatment recommendation or a broad claim that icosabutate succeeds or fails. Any conclusion should remain bounded by this phase 2b trial, its endpoint definition, the 52-week timeframe, and the information documented in the registry record.

18. Why This Trial Matters Statistically

This trial is statistically informative because it places two icosabutate dose groups alongside placebo in a randomized, masked, parallel-group design and reports a defined biopsy-based primary endpoint. The reported arm percentages allow a direct view of observed response frequency, while the sponsor’s odds ratios and the unadjusted recalculated risk differences show how the comparison depends on the chosen effect scale and analysis method.

The contrast between point estimates and their uncertainty is especially important. Response percentages are numerically higher in the icosabutate groups, but both the recalculated risk-difference intervals and sponsor-reported odds-ratio intervals include their respective null values. This illustrates why a favorable-looking point estimate is not enough: an estimate must be considered together with its precision and the method that produced it.

The study also raises practical interpretation issues common in clinical research. The primary endpoint depends on biopsy availability and a defined modified intent-to-treat population; safety denominators differ from efficacy denominators; and multiple secondary outcomes are listed. These features make transparent reporting of populations, missing data, analysis plans, and multiplicity procedures important. Several of those details are not reported in the registry record.

The sample-size illustrations further show how planning depends on the effect one aims to detect. They are based on observed effects and stated assumptions, not the trial’s original planning assumptions. This distinction helps prevent retrospective power claims from being mistaken for evidence that an observed result is conclusive or inconclusive.

Overall, the statistical value of the record lies in showing the observed endpoint pattern and the substantial uncertainty around the comparisons, while making clear where the available registry detail limits stronger inference.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary endpoint is based on biopsy reads, and the analysis population requires baseline and Week 52, or ET if applicable, biopsy information plus eligibility under the 3-panel read paradigm. The registry does not report complete participant flow, missing biopsy reasons, reader agreement, or the methods used to handle missing endpoint data. These omissions make it difficult to assess potential selection effects in the analyzed population.

The sponsor’s primary analysis is reported as a Cochran-Mantel-Haenszel odds ratio, but the registry does not identify the strata or provide the full model specification. The independent recalculations use posted summary counts and are unadjusted; they cannot reproduce any stratified or covariate-adjusted sponsor analysis. The original statistical analysis plan and sample-size justification are not reported in the registry record.

The record lists multiple secondary measures and dose comparisons, but does not report a multiplicity strategy. Without that information, secondary p-values or apparently notable findings should not be treated as confirmatory evidence. Results for some listed secondary outcomes are not reported in the available outcome detail, so a comprehensive assessment of the pattern across all planned outcomes is not possible.

The primary outcome timeframe is 52 weeks. The registry record does not report longer-term results or establish whether the biopsy-based response is durable or associated with longer-term clinical outcomes. Safety information is presented as counts and event terms; detailed exposure, timing, relatedness, severity, and adjudication information is not reported. These limitations restrict comparisons of risk and causal attribution.

Finally, the sample-size illustrations are recalculations based on observed effects and generic assumptions. They are not the original trial design calculations. The registry does not report interim analysis details, stopping rules, or other design features that might help explain the study’s operating characteristics.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Phase 2b Study of Icosabutate in Fatty Liver Disease — NCT04052516.
• Registry record last updated 2025-02-28; status last verified 2025-02.
• Results first posted 2025-02-28.
• 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

NCT04052516 is a completed phase 2b randomized, quadruple-masked, parallel-group, placebo-controlled study of icosabutate in patients with NASH. The registry reports enrollment of 280 and a 52-week primary endpoint: percentage with NASH resolution, defined by disappearance of ballooning, lobular inflammation score 0 or 1, and no worsening of fibrosis, in the 3-Panel Modified Intent-To-Treat population.

The posted response percentages were 8.7% for placebo, 17.3% for icosabutate 300mg, and 20.8% for icosabutate 600mg. The recalculated unadjusted comparisons and sponsor-reported odds-ratio analyses both retain uncertainty around the group contrasts. Secondary measures cover fibrosis, liver tests, biomarkers, and insulin resistance. The registry record does not report several details needed for a full appraisal, including the complete statistical plan, multiplicity handling, missing-data methods, and original sample-size justification.