To Evaluate the Efficacy and Safety of Nemolizumab for 12 Weeks in Participants With Chronic Kidney Disease With Associated Moderate to Severe Pruritus: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for To Evaluate the Efficacy and Safety of Nemolizumab for 12 Weeks in Participants With Chronic Kidney Disease With Associated Moderate to Severe Pruritus (NCT05075408), a randomized phase 2, phase 3 study. The primary outcome is Percentage of Responders With an Improvement of Worst Itch Numeric Rating Scale (WI NRS) Greater Than and Equal to (>=) 4 From Baseline at Week 12.

2. Clinical Question

The trial record describes a study of efficacy and safety over 12 weeks in people with chronic kidney disease and associated moderate to severe pruritus. The clinical question is therefore specific to itch intensity and the recorded response criterion at the end of that treatment period. It is not a general assessment of every symptom, longer-term outcome, or all people with chronic kidney disease.

The primary outcome is a responder percentage rather than a mean change in itch score. A participant counted as a responder only if the WI NRS improvement reached the specified threshold and the participant did not use rescue therapies or discontinue treatment because of lack of efficacy or a study-drug-related adverse event or death. The response definition thus incorporates both the itch score and specified post-randomization events.

The trial enrolled 258 participants overall. The posted primary outcome reports group sizes of 88 for nemolizumab 30 mg, 85 for nemolizumab 60 mg, and 85 for placebo. The question addressed by the statistical comparisons is whether responder percentages differed between each dose group and placebo, with the registry also reporting stratified analyses.

3. Trial Design

This was a multicenter, randomized, double-blind, parallel-group, placebo-controlled study. The registry lists the phase as Phase 2 and Phase 3. The study enrolled 258 participants and is marked completed. The recorded study start was 2022-03-18, and the primary completion date was 2024-01-04.

Participants were assigned to nemolizumab 30 mg, nemolizumab 60 mg, or placebo. The registry’s primary outcome summary describes an adult hemodialysis population with moderate to severe pruritus and a 12-week treatment period. Although the record identifies the study as multicenter, the number and locations of study sites are not reported in the registry record.

Double blinding is intended to limit differences in expectations or assessment that could arise if participants or study personnel knew treatment assignments. Random allocation is intended to reduce systematic differences between groups at entry. These are general design principles; the registry record does not report additional details about how allocation was generated, concealed, or maintained.

The primary endpoint was assessed at Week 12, with baseline used as the reference for improvement. Secondary outcomes included itch responder thresholds at Week 12 and Week 4, as well as sleep-disturbance response outcomes. The posted primary endpoint analysis used the intention-to-treat population, defined as all randomized participants. The registry record does not report the trial’s original sample-size justification, detailed allocation procedures, or a full protocol-level schedule of assessments.

The group sizes reported for the primary endpoint are 88, 85, and 85. Safety results use different at-risk group sizes: 86, 84, and 85, respectively. These are the populations attached to the respective posted outcomes and should not be treated as interchangeable denominators.

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: A total of 258 participants were enrolled and treated in this study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT population consisted of all randomized participants.

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 intent-to-treat (ITT) population included all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Responders With an Improvement of Worst Itch Numeric Rating Scale (WI NRS) Greater Than and Equal to (>=) 4 From Baseline at Week 12, measured over Baseline, Week 12.

The primary endpoint is the percentage of participants who had an improvement of at least 4 points in the Worst Itch Numeric Rating Scale from baseline at Week 12. The WI NRS asks participants to rate the intensity of their worst itch during the previous 24 hours on a scale from 0, no itch, to 10, the worst itch imaginable. Higher scores indicate worse itch.

The endpoint is binary: each participant either met the responder definition or did not. Response required the specified score improvement, no use of rescue therapies, and no treatment discontinuation due to lack of efficacy or a study-drug-related adverse event or death. As a result, the endpoint reflects more than a score change alone. A participant who met the itch-score criterion but had one of the specified events would not qualify as a responder under the registry definition.

A responder percentage is useful for presenting how often a prespecified level of improvement occurred in each group. It is different from the average change in score: it does not show the full distribution of individual score changes, and it does not distinguish people with larger improvements from those who just met the response threshold. The threshold gives the endpoint a direct, interpretable criterion, while the binary format necessarily compresses variation in the underlying ratings.

For missing primary endpoint data due to discontinuation before Week 12 or another reason, including insufficient electronic diary completion, the registry reports multiple imputation under a missing-at-random assumption, with results combined using Rubin’s formulae. The consequences of that assumption depend on the unobserved outcomes and are not established by the reported response percentages alone.

7. Results Posted in the Registry

• Nemolizumab 30 mg: 38.6% (34/88) versus 32.9% (28/85) on control; risk difference 5.7 percentage points (95% CI -8.6 to 20.0), risk ratio 1.17 (0.78–1.75); unadjusted two-proportion z-test p = 0.435.
• Nemolizumab 60 mg: 48.2% (41/85) versus 32.9% (28/85) on control; risk difference 15.3 percentage points (95% CI 0.7 to 29.9), risk ratio 1.46 (1.01–2.13); unadjusted two-proportion z-test p = 0.042.

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 Responders With an Improvement of WI NRS >= 3 From Baseline at Week 12

• 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:
  • Nemolizumab 30 mg: 48.9% (43/88) versus 47.1% (40/85) on control; risk difference 1.8 percentage points (95% CI -13.1 to 16.7), risk ratio 1.04 (0.76–1.42); unadjusted two-proportion z-test p = 0.812.
  • Nemolizumab 60 mg: 61.2% (52/85) versus 47.1% (40/85) on control; risk difference 14.1 percentage points (95% CI -0.7 to 28.9), risk ratio 1.30 (0.98–1.72); unadjusted two-proportion z-test p = 0.065.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nemolizumab 30 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nemolizumab 60 mg and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Responders With an Improvement of WI NRS >= 4 From Baseline at Week 4

• 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:
  • Nemolizumab 30 mg: 23.9% (21/88) versus 7.1% (6/85) on control; risk difference 16.8 percentage points (95% CI 6.4 to 27.2), risk ratio 3.38 (1.43–7.96); unadjusted two-proportion z-test p = 0.002.
  • Nemolizumab 60 mg: 27.1% (23/85) versus 7.1% (6/85) on control; risk difference 20.0 percentage points (95% CI 9.1 to 30.9), risk ratio 3.83 (1.64–8.94); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Nemolizumab 30 mg 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 proportion with the event is statistically higher for Nemolizumab 60 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Responders With an Improvement of Sleep Disturbance Numerical Rating Scale (SD NRS) >= 4 From Baseline at Week 12

• 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:
  • Nemolizumab 30 mg: 27.3% (24/88) versus 25.9% (22/85) on control; risk difference 1.4 percentage points (95% CI -11.8 to 14.6), risk ratio 1.05 (0.64–1.73); unadjusted two-proportion z-test p = 0.836.
  • Nemolizumab 60 mg: 42.4% (36/85) versus 25.9% (22/85) on control; risk difference 16.5 percentage points (95% CI 2.4 to 30.5), risk ratio 1.64 (1.06–2.53); unadjusted two-proportion z-test p = 0.024.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nemolizumab 30 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 Nemolizumab 60 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary results cover additional itch-response thresholds, an earlier Week 4 assessment, and sleep-disturbance response at Week 4 and Week 12. Across these endpoints, the pattern is mixed: some sponsor-reported adjusted comparisons have intervals that exclude zero, while others do not. This means the secondary results do not form a uniformly consistent pattern across every outcome, dose group, and assessment time.

These outcomes add context to the primary Week 12 itch response, but they are not substitutes for it. The primary endpoint was specifically the Week 12 WI NRS response at the more stringent recorded improvement threshold, subject to the responder definition. Other thresholds or time points ask related but different questions. Sleep-disturbance response is also a distinct patient-reported outcome rather than a direct replication of the primary itch measure.

Individual secondary p-values generally carry less confirmatory weight when many endpoints, groups, or time points are examined unless the analysis plan specifies how the overall false-positive risk is controlled. General explanation: testing multiple hypotheses creates more opportunities for a result to appear statistically notable by chance. The registry record does not report a multiplicity procedure or a hierarchy governing the secondary outcomes. Therefore, the secondary p-values should be read as endpoint-specific evidence rather than as a single controlled test of a broad treatment claim.

The record lists five posted secondary outcomes and twelve analyses overall, but those counts alone do not establish which results were prespecified as confirmatory or how they were intended to inform the primary question. The secondary findings can help describe whether response patterns extend across outcomes and timing, while the missing multiplicity details limit how strongly isolated findings should be interpreted.

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

• Percentage of Responders With an Improvement of WI NRS >= 3 From Baseline at Week 12
• Percentage of Responders With an Improvement of WI NRS >= 4 From Baseline at Week 4
• Percentage of Responders With an Improvement of Sleep Disturbance Numerical Rating Scale (SD NRS) >= 4 From Baseline at Week 12
• Percentage of Responders With an Improvement of WI NRS >= 3 From Baseline at Week 4
• Percentage of Responders With an Improvement of SD NRS >= 4 From Baseline at Week 4

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a binary outcome: a participant is classified as a responder or not, and the group result is expressed as a percentage. A comparison of binary outcomes can be expressed as a risk difference, a risk ratio, or an odds ratio. These measures answer related but different questions. The risk difference describes the absolute separation between response probabilities; the risk ratio compares those probabilities as a relative quantity; and the odds ratio compares the odds of response. The registry’s reported primary analysis is expressed as a stratified adjusted percentage difference.

What does stratification add?

General explanation: a stratified analysis compares groups within categories defined by one or more factors and then combines information across those categories. This can account for the stratification factors used in the analysis and may differ from a crude comparison that treats all participants as one unstratified group. The registry names the Cochran-Mantel-Haenszel method for the reported analyses. It does not identify the stratification factors in the posted results, so their specific role cannot be described from the registry record.

The sponsor-reported primary comparisons are a 7.0 adjusted percentage difference for nemolizumab 30 mg versus placebo and a 14.5 adjusted percentage difference for nemolizumab 60 mg versus placebo. The corresponding 97.5% confidence intervals and p-values are reported separately for each comparison. The percentage-difference scale in that analysis is not the same display as the decimal risk-difference values in the simple unadjusted re-calculations; they arise from different analysis approaches and should not be treated as interchangeable estimates.

What does the confidence interval convey?

General explanation: a confidence interval describes the uncertainty around an estimated effect under the assumptions of the analysis. A wider interval indicates less precision than a narrower interval. An interval that includes zero for a difference is compatible with no difference under the interval’s construction, while also allowing effects in either direction if its limits extend to both sides of zero. A confidence interval is not a guarantee that the true effect lies within its limits, nor does it report the probability that a particular hypothesis is true.

The registry reports 97.5% confidence intervals for its adjusted analyses. The primary endpoint intervals extend from negative to positive values for both dose comparisons. The p-values are another way of expressing the degree of compatibility between the observed data and a null hypothesis, under the test’s assumptions. They do not measure the probability that the null hypothesis is true, and a p-value alone does not describe the size or precision of the effect.

Why do the recalculated results differ?

The simple unadjusted re-calculations use posted summary counts to make a basic comparison without the sponsor’s stratified adjustment. They therefore answer a related but not identical analytical question. Differences between the recalculated and reported estimates or p-values can arise because the approaches use different adjustment structures and statistical procedures. The registry’s reported analyses are the sponsor’s own analysis and take precedence where the discrepancy is flagged. The unadjusted calculations should be read as supplementary checks, not as corrections to the reported analysis.

How are missing outcomes handled?

The registry says missing primary endpoint data due to early discontinuation or other reasons were imputed using multiple imputation under a missing-at-random assumption. General explanation: multiple imputation creates more than one plausible completed dataset, analyzes each one, and combines the estimates to reflect both within-dataset and between-dataset uncertainty. Rubin’s formulae are identified as the combination method. The missing-at-random assumption means, in broad terms, that missingness can be accounted for by observed information in the model; it does not mean that missingness is unrelated to outcomes in every circumstance. The variables used in the imputation model and sensitivity analyses are not reported in the registry record.

What cannot be inferred from the analysis listing?

The record lists six outcome measures, five posted secondary outcomes, and twelve analyses. Those counts do not reveal which tests were designated as confirmatory, how testing across endpoints or dose groups was controlled, or whether an ordered testing strategy was used. Such statistical-plan details are not reported in the registry record. Likewise, the record does not report interim analyses or the original sample-size assumptions. Statistical interpretation should therefore distinguish the posted estimates from unreported design or analysis choices.

11. Confidence Intervals and Precision

The registry’s primary endpoint confidence intervals are broad enough to include both negative and positive adjusted differences. For nemolizumab 30 mg versus placebo, the sponsor-reported adjusted difference is 7.0, with a 97.5% confidence interval from -10.6 to 24.6. For nemolizumab 60 mg versus placebo, it is 14.5, with a 97.5% confidence interval from -3.1 to 32.2. Both intervals include zero, indicating that the reported estimates do not pin down the direction of the adjusted difference with high precision.

Confidence interval width is important because the point estimate is only one plausible summary of the data. A confidence interval includes a range of effect sizes compatible with the data and analysis assumptions. The primary intervals allow for no adjusted difference and for differences in either direction. This uncertainty means that the point estimates should not be read as exact or definitive measurements of the underlying group differences.

The unadjusted re-calculated intervals are also informative about the distinction between analyses: -0.086 to 0.200 for the 30 mg comparison and 0.007 to 0.299 for the 60 mg comparison. These are not the sponsor-reported adjusted intervals, and the flagged discrepancy means the sponsor’s own analyses take precedence.

Precision depends in part on the number of participants with outcome information and the variability in the data. The primary endpoint group sizes were 88, 85, and 85. The registry reports multiple imputation for missing primary endpoint outcomes, but the extent and pattern of missingness are not described in the record. The confidence intervals should therefore be interpreted within the reported analysis and its assumptions, rather than as a complete account of every uncertainty in study conduct or generalizability.

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 observed effects, not the trial’s original design calculations. For these binary outcomes, the listed figures are participants per arm, not total participants and not total events. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect.

The 80% power column gives the planned number of participants per arm under which a study would have an 80% chance of detecting the specified effect, if the assumptions used for that calculation hold. The 90% power column uses a higher target chance of detecting that effect and therefore generally calls for more participants per arm. These are planning concepts, not guarantees about the result of a future study.

Rows for 100%, 75%, and 50% of the observed effect illustrate how the participant requirement changes when the effect being planned for is smaller than the observed estimate. A smaller target effect generally requires more participants to detect with the same power and significance assumptions. The figures are sensitive to the observed effect used as their starting point, so they should not be taken as stable estimates of the sample size needed for every future study.

The original trial’s sample-size justification and design assumptions are not reported in the registry record. These illustrations are not observed power: they do not calculate the probability that the completed trial detected an effect, and they do not change the interpretation of the sponsor-reported endpoint analysis.

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 = 0.329; treatment proportion p₁ = 0.386; average p̄ = 0.358.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6779 = 1.3287.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6767 = 0.5696.
4. n = (1.3287 + 0.5696)² / (0.0570)² = 1,111.0, rounded up to 1,112 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 <- 0.329411764705882                          # control proportion
p1 <- 0.386363636363636                          # 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(5075408)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 1,112 (80% power), 1,487 (90% power)
 75% of observed effect: n per arm = 1,959 (80% power), 2,621 (90% power)
 50% of observed effect: n per arm = 4,366 (80% power), 5,844 (90% power)
power.prop.test: 1111 
Simulated power at n = 1,112 per arm: 0.797 (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 sponsor analyses using the Cochran-Mantel-Haenszel method and describes the estimates as stratified adjusted percentage differences. For the primary endpoint, the reported adjusted differences are 7.0 for nemolizumab 30 mg versus placebo and 14.5 for nemolizumab 60 mg versus placebo, with 97.5% confidence intervals and p-values reported for each comparison.

The posted summary counts also allow simple unadjusted re-calculations. Those calculations produce different estimates and p-values from the sponsor’s analyses, because they are unadjusted comparisons rather than the reported stratified analyses. The registry record flags a discrepancy between the sponsor-reported results and the re-calculations. The sponsor’s own analysis takes precedence; the recalculated results are useful only as supplementary, unadjusted comparisons.

This distinction matters when reading the inference. The adjusted primary confidence intervals both include zero, and the sponsor-reported p-values are 0.370 and 0.069. The unadjusted comparison for the 60 mg group has p = 0.042, but that result does not replace the sponsor’s adjusted result. The estimates should not be mixed across methods or selected according to which appears more favorable.

The registry record does not report enough detail to reconstruct all features of the sponsor’s analysis, including the specific stratification factors. Thus, the reported sponsor analysis is the principal inferential result, while the unadjusted re-calculation provides a separate descriptive check.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several statistical hypotheses are tested, such as comparisons across more than one dose, outcome, or assessment time. General explanation: as the number of tests increases, the chance of at least one apparently notable result can also increase if each test is judged separately. Statistical plans may address this through adjusted significance thresholds, a testing hierarchy, or other procedures. The registry record does not report whether or how multiplicity was controlled for the primary comparisons or secondary endpoints.

The primary endpoint includes two dose comparisons with placebo, and the record also lists five posted secondary outcomes. There are twelve analyses listed overall. These registry entries make the missing multiplicity details relevant to interpretation, but the counts do not reveal the planned testing family or which results were intended to support formal conclusions. The reported 97.5% confidence intervals should be read as the registry presents them; the record does not explain the choice of confidence level or how it relates to the analysis plan.

For the primary endpoint, the record specifies an intention-to-treat population consisting of all randomized participants. It also describes a responder definition that excludes participants with rescue therapy or treatment discontinuation for specified reasons. Missing data due to discontinuation before Week 12 or other reasons were handled by multiple imputation under a missing-at-random assumption, with results combined using Rubin’s formulae.

The registry record does not report the imputation model variables, the amount of missing primary endpoint data, or sensitivity analyses exploring departures from the missing-at-random assumption. It also does not report a per-protocol analysis or other population-specific primary analysis. These omissions leave uncertainty about the robustness of the missing-data approach and the role of alternative analysis populations. They do not negate the posted results, but they define what can be assessed from the registry record alone.

Interim analyses, any stopping rules, and the full statistical analysis plan are not reported in the registry record. Accordingly, interpretation should avoid assumptions about those procedures or about the planned handling of multiple outcomes.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (5.9%), acute myocardial infarction (4.7%), hypervolaemia (4.7%), cardiac arrest (3.5%), hyperkalaemia (3.5%).

The registry reports serious adverse event counts for the safety groups: 33 of 86 participants in the nemolizumab 30 mg group, 22 of 84 in the nemolizumab 60 mg group, and 27 of 85 in the placebo group. Other, non-serious adverse event counts are 29 of 86, 25 of 84, and 19 of 85, respectively. Deaths recorded are 4, 4, and 5, respectively.

These figures are counts of participants affected in the posted safety groups. They are not adjusted comparisons, and they do not by themselves establish that an event was caused by study treatment. The registry record lists serious adverse event terms including pneumonia at 5.9%, acute myocardial infarction at 4.7%, hypervolaemia at 4.7%, cardiac arrest at 3.5%, hyperkalaemia at 3.5%, and sepsis at 2.4%.

Safety counts should be considered in light of the group sizes, follow-up period, event definitions, and the underlying clinical context. The record does not give a full narrative for each event, timing, recurrence, or detailed causal assessments. The posted figures therefore describe reported events during the study and are not, on their own, a complete comparative safety analysis.

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

The results describe responder percentages and statistical comparisons for adults receiving hemodialysis who had chronic kidney disease associated with moderate to severe pruritus. The primary endpoint concerns a specified improvement in worst itch at Week 12, with additional conditions in the responder definition. It is a focused outcome, not a comprehensive measure of health or of all consequences of chronic kidney disease.

The sponsor-reported adjusted primary confidence intervals include zero for both dose comparisons with placebo. The posted results therefore leave meaningful uncertainty about the size and direction of the adjusted difference. The unadjusted re-calculations do not match the sponsor’s analysis, and the sponsor’s own analysis takes precedence where the discrepancy is flagged. These statistical results should not be reduced to a simple claim based only on the observed percentages or on one p-value.

The study record does not establish how long any observed response might persist beyond the assessed period, nor does it report outcomes outside the posted measures. The study’s stated treatment period was 12 weeks. The record also does not report a clinically important between-group difference threshold, so the clinical importance of a particular estimate cannot be determined from the statistical results alone.

The findings should not be assumed to apply to people who do not match the recorded study population, including those who are not receiving hemodialysis or do not have the specified degree of pruritus. The trial’s group comparisons are evidence about the enrolled study population and analysis, not a guarantee about an individual’s outcome. Statistical uncertainty, missing-data assumptions, and unreported multiplicity details all matter when deciding how much weight to place on the results.

Safety counts provide a description of reported events in each group, but do not independently establish causation or provide a complete assessment of comparative risk. The results are most appropriately read as a bounded account of the specific outcomes and period recorded in this trial.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be interpreted through the endpoint definition, analysis method, and uncertainty together. The primary outcome is not simply a change in an itch score: it is a responder classification that incorporates the improvement threshold, rescue therapy, and specified treatment discontinuations. The meaning of the reported percentages depends on those rules.

It also shows why adjusted and unadjusted analyses should remain distinct. The registry reports stratified analyses, while a basic re-calculation from summary counts gives different results for one comparison. When the record flags a discrepancy, the sponsor’s own analysis takes precedence. A difference between methods is a reason to identify the estimand and analytical approach, not to choose whichever result appears more favorable.

Precision is another central issue. The sponsor-reported confidence intervals for the primary comparisons include zero and span a range of possible adjusted differences. That range is more informative than a point estimate alone and emphasizes that the data do not identify a single exact effect.

The secondary outcomes make the interpretation more complex because they span different response thresholds, times, and symptom domains. Without a reported multiplicity procedure, isolated secondary findings need cautious interpretation. Missing-data assumptions are also consequential: the record describes multiple imputation under a missing-at-random assumption but does not report the imputation model or sensitivity analyses.

Finally, planning illustrations based on observed effects are distinct from the completed trial’s original design rationale and from observed power. Keeping these concepts separate helps prevent retrospective calculations from being mistaken for evidence that the original study was or was not adequately designed.

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 a dichotomized response measure. It does not show the full distribution of WI NRS scores or the amount of improvement among participants who met the threshold. The responder definition also excludes participants meeting specified criteria for rescue therapy or treatment discontinuation, so the endpoint reflects both symptom ratings and these events.

The analysis uses multiple imputation for missing primary endpoint observations under a missing-at-random assumption. The registry record does not report the extent or pattern of missingness, the model variables, or sensitivity analyses. The effect of departures from the imputation assumption therefore cannot be assessed from the posted information.

The sponsor’s adjusted primary comparisons and the simple unadjusted re-calculations differ, and the record flags this discrepancy. The specific stratification factors used in the sponsor’s analysis are not reported in the registry record, which limits independent interpretation of the adjustment. The sponsor analysis takes precedence, but the methodological difference remains relevant to understanding why estimates vary.

The registry record does not report multiplicity handling for the two primary dose comparisons and multiple secondary outcomes. It also does not report the original sample-size justification, interim analyses, full statistical analysis plan, or detailed allocation procedures. These missing details constrain assessment of the planned inferential framework.

The stated treatment period and primary assessment are limited to 12 weeks. The record does not establish longer-term response or safety. Generalization is also limited by the described population: adults receiving hemodialysis with moderate to severe chronic kidney disease-associated pruritus. The posted safety information consists of counts and selected serious adverse event terms, without detailed event-level narratives or complete causal assessments.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: To Evaluate the Efficacy and Safety of Nemolizumab for 12 Weeks in Participants With Chronic Kidney Disease With Associated Moderate to Severe Pruritus — NCT05075408.
• Registry record last updated 2026-05-01; status last verified 2025-01.
• Results first posted 2025-02-20.
• 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

NCT05075408 is a completed, multicenter, randomized, double-blind, parallel-group, placebo-controlled study listed as Phase 2 and Phase 3. It enrolled 258 participants and evaluated nemolizumab 30 mg, nemolizumab 60 mg, and placebo in adults receiving hemodialysis with moderate to severe chronic kidney disease-associated pruritus over a 12-week period.

The primary endpoint was the percentage of responders with at least a 4-point improvement in worst itch from baseline at Week 12, subject to additional rescue-therapy and discontinuation criteria. Sponsor-reported stratified adjusted analyses gave confidence intervals that included zero for both dose comparisons with placebo. Simple unadjusted re-calculations differ; the sponsor’s own analysis takes precedence because the discrepancy is flagged.

The registry also reports secondary itch and sleep-disturbance outcomes, adverse event counts, and a multiple-imputation approach for missing primary outcomes. Multiplicity procedures, the original sample-size justification, and several analysis details are not reported in the registry record.