A Phase IIb Study to Evaluate the Safety of Zibotentan/Dapagliflozin in Participants With Cirrhosis-ZEAL-UNLOCK: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase IIb Study to Evaluate the Safety of Zibotentan/Dapagliflozin in Participants With Cirrhosis-ZEAL-UNLOCK (NCT06269484), a randomized phase 2 study. The primary outcome is Cumulative Number of Subjects With Any of the Components of the Composite Endpoint: >2kg Increase in Body Weight (Office-based), >2 L Increase in Total Body Water, Increase in 2 or More Loop-diuretic Equivalents, Fluid Retention Adverse Event (AE).

2. Clinical Question

3. Trial Design

ZEAL-UNLOCK (NCT06269484) is registered as a phase IIb, randomised, parallel-group, placebo-controlled study in participants with liver cirrhosis. The registry describes the study as multicentre and double-blind; its masking classification is triple. The trial status is completed. The registry lists a start date of 2024-02-15 and a primary completion date of 2024-12-11.

Three groups were planned: zibotentan plus dapagliflozin, zibotentan plus a placebo matching dapagliflozin, and placebo matching both study medicines. Each regimen was once daily for 6 weeks. Dapagliflozin was listed at 10 mg in the combination arm. This design permits comparisons of the combination with zibotentan monotherapy and of each active regimen with placebo. The record reports results for those pairwise comparisons, although it does not establish that every possible comparison was the primary statistical contrast.

The registry reports 73 enrolled participants, while the primary endpoint results list 24 participants in each arm. The primary analysis population is described as all randomised participants who received at least one dose. The record does not explain the relationship between the overall enrollment figure and the number represented in the arm-level endpoint results, so no reason for that difference can be inferred. The original sample-size justification, intended statistical power, and design assumptions are not reported in the registry record. The planning illustrations based on observed effects are separate from those original trial-design decisions.

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: Of 88 study participants, 73 met inclusion criteria and were not withdrawn by subject and subsequently randomised to treatment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomised subjects who received at least one dose of treatment are included in the analysis. For intercurrent events treatment policy strategy was used. No imputation was performed.

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: Randomised subjects who received at least one dose of treatment.

6. Primary Endpoint

The registry lists the primary outcome as Cumulative Number of Subjects With Any of the Components of the Composite Endpoint: >2kg Increase in Body Weight (Office-based), >2 L Increase in Total Body Water, Increase in 2 or More Loop-diuretic Equivalents, Fluid Retention Adverse Event (AE), measured over baseline to Week 6.

The primary endpoint counts participants with any of four specified fluid-retention events between baseline and Week 6. It is a composite: a participant is counted if at least one component occurs. The components cover changes in office-based body weight and total body water, greater use of loop-diuretic equivalents, and a fluid-retention adverse event. The registry defines the outcome as a cumulative number of participants with an event.

A composite can capture several ways a clinical state may be expressed and can produce a single count for comparison across groups. Its interpretation depends on which components are included and whether those components are similarly meaningful. The registry lists the four components, but does not report their separate primary-endpoint counts in the registry record. Consequently, the overall composite counts cannot show which component contributed most to the group totals, whether components overlapped within participants, or whether the pattern was consistent across components.

The registry states that the primary endpoint timeframe was baseline to Week 6. It describes the analysis population as all randomised participants who received at least one dose and says a treatment-policy strategy was used for intercurrent events, with no imputation performed. These details specify the posted approach, but do not answer every question about how individual events were identified or adjudicated; such details are not reported in the registry record.

7. Results Posted in the Registry

• Zibo/Dapa: 58.3% (14/24) versus 25.0% (6/24) on control; risk difference 33.3 percentage points (95% CI 7.1 to 59.6), risk ratio 2.33 (1.08–5.04); unadjusted two-proportion z-test p = 0.019.
• Zibo: 58.3% (14/24) versus 25.0% (6/24) on control; risk difference 33.3 percentage points (95% CI 7.1 to 59.6), risk ratio 2.33 (1.08–5.04); unadjusted two-proportion z-test p = 0.019.

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.

Cumulative Number of Subjects With Either of the Two Components of This Composite: 1. >3 L Increase in Total Body Water Volume From Baseline to Week 6 2. Increase in 3 or More Loop-diuretics Equivalents Use

• 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:
  • Zibo/Dapa: 29.2% (7/24) versus 8.3% (2/24) on control; risk difference 20.8 percentage points (95% CI -0.4 to 42.1), risk ratio 3.50 (0.81–15.16); unadjusted two-proportion z-test p = 0.064.
  • Zibo: 37.5% (9/24) versus 8.3% (2/24) on control; risk difference 29.2 percentage points (95% CI 6.9 to 51.5), risk ratio 4.50 (1.08–18.69); unadjusted two-proportion z-test p = 0.016.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Zibo/Dapa 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 Zibo than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes spanning body weight, body fat mass, total body water, extracellular and intracellular water, weight over time, loop-diuretic-equivalent use, and a composite involving total body water increase or increased loop-diuretic use. These outcomes provide related but distinct views of fluid status and body composition. They should not be assumed to measure the same underlying feature as the primary composite.

The posted secondary composite analysis has a broad directional pattern in which event counts are higher in the active-treatment groups than in placebo. The comparison estimates are not uniform in their precision: one recalculated active-versus-placebo interval includes zero, while the other does not. The registry’s sponsor-reported comparisons for this secondary outcome are limited to two pairings. This collection of findings may be considered alongside the primary result, but it does not independently confirm the primary result or identify which component accounts for the pattern.

The registry lists 10 posted secondary outcomes. A broad list of outcomes increases the number of opportunities to observe a seemingly notable result by chance, especially when several comparisons are examined. Unadjusted secondary results carry less weight because the multiplicity approach and outcome hierarchy are not reported in the registry record. Without that information, the reader cannot tell whether a result was one of many exploratory analyses or a prespecified test with a controlled error rate.

Secondary outcomes are useful for describing complementary measurements, but they do not repair limitations in the primary comparison. Their interpretation depends on how they were defined, when they were measured, how missing observations were handled, and whether the analyses were planned in advance. The registry record does not give enough detail to resolve those questions. The overall pattern is therefore descriptive and should be treated as supporting context rather than definitive evidence about any one secondary measure.

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

• Change From Baseline in Body Weight
• Change From Baseline in Body Fat Mass
• Change From Baseline in Total Body Water
• Change From Baseline in Extracellular Water Volume
• Change From Baseline in Intracellular Water Volume
• Change in Body Weight (kg) Over Time Course of Study
• Change in Total Dosage of Loop-diuretic Equivalents Use
• Cumulative Number of Subjects With Either of the Two Components of This Composite: 1. >3 L Increase in Total Body Water Volume From Baseline to Week 6 2. Increase in 3 or More Loop-diuretics Equivalents Use

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: a participant either met at least one component of the composite or did not. The registry reports the number of participants with an event in each arm and describes its comparison method as proportions used for comparison. Its reported effect measure is the risk difference (RD), expressed as the event proportion in one group minus the event proportion in the other group. The direction depends on the order of the groups in the comparison.

What does a risk difference describe?

General: a risk difference expresses the absolute separation between two event proportions. A value of zero indicates equal observed proportions under the chosen ordering; a positive or negative value indicates which group has the larger proportion. Unlike a relative measure, it stays on the proportion scale. Its interpretation still depends on the endpoint definition, the groups being compared, and the precision of the estimate.

For the primary endpoint, the registry reports a risk difference of 0.33 for the combination-versus-placebo comparison and 0.33 for zibotentan-versus-placebo. It reports a risk difference of 0 for combination versus monotherapy. These are sponsor-posted estimates. Recalculations from the displayed event counts are unadjusted and should be understood as checks based on summary data, rather than as adjusted analyses or replacements for the sponsor’s analysis. The recalculated unadjusted p-value for each active-versus-placebo comparison is 0.019.

How should the uncertainty measures be read?

General: a confidence interval communicates the precision of an estimate under a statistical procedure and its assumptions. Wider intervals indicate less precision than narrower intervals. An interval spanning zero for a risk difference is compatible with no difference as well as with differences in either direction at that interval’s stated confidence level. An interval wholly on one side of zero indicates that the corresponding interval procedure does not include zero. These statements do not establish causation or importance.

The registry reports 90% confidence intervals for the sponsor’s primary risk differences. It does not list p-values alongside those sponsor comparisons. Separately, the recalculation includes intervals and unadjusted p-values; the confidence level for those recalculated intervals is not specified in the registry entries, so it should not be assumed. The reported sponsor intervals and recalculated intervals need not match exactly because the calculations can use different procedures.

What does unadjusted mean?

General: an unadjusted comparison does not account for other variables or for the fact that many comparisons may be examined. The registry describes the reported comparison method in terms of proportions and risk differences, but does not report covariate adjustment for these results. The analysis plan, any adjustment for multiple comparisons, and the exact statistical procedure behind the sponsor intervals are not reported in the registry record. A p-value from a simple recalculation therefore answers only the narrow comparison under that calculation’s assumptions.

The primary population is described as all randomised participants who received at least one dose of treatment. The registry states that a treatment-policy strategy was used for intercurrent events and that no imputation was performed. General: a treatment-policy strategy aims to interpret outcomes according to assigned treatment despite certain events after randomisation; the exact handling depends on the protocol’s definitions. No imputation means missing values were not filled in through an imputation procedure, but does not, on its own, reveal the amount or pattern of missing data. Missing-data counts and details are not reported in the registry record.

Other analyses include secondary outcomes and safety summaries. The secondary results include comparisons of proportions for one posted binary composite; the registry also lists outcomes involving weight, body composition, body water, and loop-diuretic use. These analyses have different endpoint definitions and should not be treated as interchangeable with the primary composite. Whether they were prespecified, how they were prioritized, or how multiplicity was handled is not reported in the registry record.

The planning illustrations are a separate exercise based on the observed effect and stated planning assumptions. General: a power calculation estimates the sample size associated with a target probability of detecting an assumed effect under specified conditions. It does not describe the probability that this completed trial’s results are correct. The stated illustration uses a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The target effect is a stated fraction of the observed effect. These calculations are not evidence about the trial’s original protocol rationale, which is not reported in the registry record.

11. Confidence Intervals and Precision

The primary endpoint counts are based on 24 participants in each arm. With arm sizes of this scale, a change in the event status of a small number of participants can noticeably alter the observed proportions and their comparison. The estimates should therefore be read with their intervals, rather than as exact descriptions of a stable underlying difference.

The sponsor reports a risk difference of 0.33 for each active group versus placebo, with a 90% confidence interval from 0.09 to 0.55 in each comparison. Those intervals do not include zero, but their span indicates uncertainty about the magnitude of the difference. The combination-versus-monotherapy estimate is 0, with a 90% confidence interval from -0.24 to 0.24. That interval includes zero and permits a range of possible group differences in both directions. It does not demonstrate that the treatments are equivalent; an equivalence conclusion would require a prespecified margin and an appropriate design, neither of which is reported in the registry record.

General: confidence intervals express uncertainty conditional on the data and method. They do not account automatically for unreported design choices, measurement error, selective reporting, or multiplicity. They also do not describe the distribution of individual outcomes. A point estimate is the centre of the reported comparison, while the interval shows how much uncertainty remains under its procedure.

The registry’s 90% intervals are distinct from the intervals accompanying the recalculated comparisons. The confidence level for the latter is not stated in the registry entries, so the sponsor intervals are the clearest level-labelled precision estimates for the posted primary analyses. The registry does not report component-specific primary counts, missing-data patterns, or a detailed account of model assumptions; each limits further assessment of precision and robustness.

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 express the required number of participants per arm for comparisons of two groups. They are not total trial enrollment figures and are not counts of events. The assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and a target effect equal to the stated fraction of the observed effect. The original trial-design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a design with an 80% chance of detecting the assumed effect if that effect were the true one, under the calculation’s assumptions. The 90% power column gives the corresponding estimate for a 90% chance. Power is a design property conditional on assumptions; it does not describe the probability that the observed result is true. These figures are planning illustrations, not observed power for the completed trial.

Rows that use 100% of the observed effect assume an effect as large as the one seen in the trial. Rows using 75% or 50% represent smaller target effects. Smaller effects are harder to distinguish from random variation and therefore require more participants per arm under the stated assumptions. For the primary comparison, the illustration lists 34 and 44 participants per arm for 80% and 90% power, respectively, when using 100% of the observed effect; at 75% it lists 58 and 77, and at 50% it lists 125 and 167. These are not recommendations or guarantees, and they do not establish what enrollment the original study required.

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 = 0.250; treatment proportion p₁ = 0.583; average p̄ = 0.417.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6972 = 1.3665.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6562 = 0.5522.
4. n = (1.3665 + 0.5522)² / (0.3333)² = 33.1, rounded up to 34 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 <- 0.25                          # control proportion
p1 <- 0.583333333333333                          # 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(6269484)
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 = 34 (80% power), 44 (90% power)
 75% of observed effect: n per arm = 58 (80% power), 77 (90% power)
 50% of observed effect: n per arm = 125 (80% power), 167 (90% power)
power.prop.test: 33.1 
Simulated power at n = 34 per arm: 0.819 (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 primary analyses report risk differences using proportions. For the combination versus placebo and zibotentan versus placebo, each posted estimate is 0.33, with a 90% confidence interval from 0.09 to 0.55. The comparison between combination and zibotentan alone is reported as 0, with a 90% confidence interval from -0.24 to 0.24. The sponsor results are the registry’s own analyses and should be read as such.

Simple unadjusted recalculations from the posted primary event counts yield p = 0.019 for each active-treatment-versus-placebo comparison. The recalculation is a check using summary counts, not an adjusted analysis and not a replacement for the sponsor’s reported estimates. Its intervals are not identical to the sponsor’s 90% intervals, and the confidence level for the recalculated intervals is not specified in the registry entries. Different statistical procedures can yield different interval limits even when based on the same counts.

The registry does not mark a discrepancy between the sponsor analysis and the recalculation. The recalculated p-values add a test statistic from a simple method, but they do not add information about the sponsor’s protocol, adjustment strategy, or analysis plan. Those details are not reported in the registry record. The sponsor’s comparisons and the recalculation should therefore remain clearly distinguished rather than blended into a single result.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary composite and multiple secondary outcomes, as well as comparisons among three treatment groups. It does not report a multiplicity adjustment, a testing hierarchy, or a prespecified order for interpreting comparisons. When several outcomes and pairwise tests are examined, the chance of at least one apparently unusual result can rise. General: multiplicity procedures are used to control or describe this risk; without a stated procedure, individual unadjusted p-values do not provide a complete account of false-positive risk across the full set of analyses.

The primary analysis population is described as all randomised participants who received at least one dose of treatment. The record says that a treatment-policy strategy was used for intercurrent events and that no imputation was performed. It does not report the count of missing endpoint observations, reasons for missingness, or a sensitivity analysis for missing data. No imputation indicates that missing values were not filled in through an imputation procedure; it does not establish that data were complete or that missingness could not affect interpretation.

The record also does not report the original sample-size calculation, its target effect, or the rationale for the enrollment target. The planning illustrations based on observed effects are not a substitute for those design details. The statistical analysis plan, adjustment variables, exact interval procedure, and any interim analyses are not reported in the registry record. No conclusions about these unreported features can be drawn from the arm counts or posted results.

These omissions matter because they constrain the reader’s ability to judge whether the analyses followed prespecified methods, how robust the results are to missing information, and how many statistical tests informed the interpretation. They do not invalidate the registry results, but they call for restraint: the posted estimates are best treated as reported comparisons with limited information about broader error control and sensitivity.

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: gastrointestinal haemorrhage (8.3%), ascites (4.2%), oesophageal varices haemorrhage (4.2%).

The registry reports serious adverse event counts of 1 among 24 participants in the zibotentan/dapagliflozin group, 2 among 24 in the zibotentan group, and 1 among 24 in the placebo group. Deaths are reported as 0 in each arm. The record also lists other adverse-event counts of 14, 15, and 4, respectively. These figures are descriptive counts, not adjusted comparisons.

The registry lists gastrointestinal haemorrhage at 8.3%, ascites at 4.2%, and oesophageal varices haemorrhage at 4.2% among the top serious terms. The record does not establish from these figures alone how an event related to treatment, nor do the counts indicate severity beyond the serious-event classification. Small group sizes and short treatment duration limit the ability of these summaries to characterize uncommon events or compare risks precisely.

Safety counts should be read alongside the registry’s event definitions and the number at risk in each arm. The posted figures do not provide a complete account of event timing, recurrence, or participant-level overlap. They describe what is recorded, rather than offering a causal assessment or a prediction for other participants.

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

The registry results describe the number of participants meeting a composite fluid-retention endpoint during the baseline-to-Week 6 period. The active-treatment groups each had 14 events among 24 participants, while placebo had 6 among 24. The sponsor’s reported risk differences versus placebo were each 0.33, with 90% confidence intervals from 0.09 to 0.55. The comparison between the active regimens had a reported risk difference of 0 and a 90% confidence interval from -0.24 to 0.24.

These findings do not identify which component of the composite drove the group counts. They do not show that every participant had the same type or severity of event, and they do not establish the cause of an event. Equal observed counts in the two active groups do not prove that the regimens are equivalent; the interval for their comparison allows for uncertainty in either direction.

The results also do not establish what would happen beyond the six-week treatment period or in populations not described by this study. The record concerns participants with cirrhosis in a phase IIb study, with 24 participants represented in each reported primary arm. The original design rationale, detailed missing-data information, and multiplicity approach are not reported in the registry record.

Statistical evidence is not the same as clinical importance. A risk difference and its interval describe observed group comparisons under a method; they do not determine whether an effect is meaningful for an individual or how a treatment should be used. These results should be understood as a limited description of the registry’s posted data, not as medical advice or a definitive assessment of treatment benefit or harm.

18. Why This Trial Matters Statistically

This trial illustrates why the endpoint definition matters as much as the headline comparison. The primary outcome combines changes in body weight, total body water, loop-diuretic use, and fluid-retention adverse events. A single composite count is compact, but it can conceal different component patterns. Without separate component counts, readers cannot tell which types of events account for the observed group totals.

It also illustrates the importance of distinguishing the sponsor’s reported analysis from a simple recalculation. The sponsor reports risk differences and 90% confidence intervals; an unadjusted recalculation from counts yields p-values. These statistics answer related but not identical questions and rely on procedures that may differ. Reporting both without conflating them helps preserve the distinction between the registry analysis and a summary-data check.

The three-arm structure permits comparisons of the combination with zibotentan alone and with placebo, as well as monotherapy with placebo. The reported primary counts are the same in the two active arms, while placebo has fewer recorded events. The small arm sizes and intervals remain central to interpreting how precisely those contrasts are estimated. A point estimate alone would obscure that uncertainty.

Finally, the record offers an example of why trial design assumptions, missing-data handling, and multiplicity plans matter. Observed-effect planning illustrations cannot recover the original sample-size rationale, and a set of unadjusted secondary findings cannot be interpreted without knowing their place in the testing plan. These considerations shape what can be learned from the results, even when the reported event counts and estimates are clear.

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 endpoint is composite, and the registry results do not report separate primary counts for its components. This prevents an assessment of whether the observed differences were concentrated in one component or spread across several. The record also does not give participant-level overlap among components, so a component-level interpretation cannot be reconstructed from the cumulative counts.

Each reported primary arm has 24 participants. Such a small number limits precision and makes estimates sensitive to a few participants’ outcomes. The follow-up timeframe is baseline to Week 6, which does not describe longer-term patterns. The registry reports 73 enrolled overall, but the reason that the primary arm results list 24 participants in each group is not reported in the registry record.

The record describes the primary population and states that no imputation was performed, but does not provide missing-observation counts, reasons, or sensitivity analyses. It also does not report the detailed analysis plan, original sample-size justification, multiplicity method, or exact statistical procedures underlying the sponsor’s intervals. These gaps limit assessment of robustness and the extent to which the posted comparisons were prespecified.

For safety, the event counts are descriptive and based on the same small arm sizes. The registry’s serious-event terms and summary counts do not show timing, recurrence, or causal attribution. More broadly, the posted secondary outcomes cover multiple related measurements, while their analysis hierarchy and error-control strategy are not reported. These limitations call for cautious, narrowly framed interpretation of the observed registry results.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Phase IIb Study to Evaluate the Safety of Zibotentan/Dapagliflozin in Participants With Cirrhosis-ZEAL-UNLOCK — NCT06269484.
• Registry record last updated 2026-01-20; status last verified 2026-01.
• Results first posted 2026-01-20.
• 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

ZEAL-UNLOCK (NCT06269484) is a completed, randomised, parallel-group, placebo-controlled phase IIb study in participants with liver cirrhosis. The registry describes double-blind conduct and triple masking. It reports 73 enrolled participants and three treatment arms, each with 24 participants in the primary endpoint results.

The primary outcome was a composite count of participants with any specified fluid-retention event from baseline to Week 6. The registry reports 14 events in each active arm and 6 in placebo. Sponsor-reported risk differences versus placebo were 0.33, with 90% confidence intervals from 0.09 to 0.55; the active-treatment comparison was reported as 0, with an interval from -0.24 to 0.24.

The record also lists secondary outcomes and adverse-event summaries. The original sample-size rationale, multiplicity approach, detailed missing-data information, and full statistical analysis plan are not reported in the registry record. The posted results therefore support a description of the recorded counts and estimates, with important limits on precision and interpretation.