Hidradenitis Suppurativa Phase 2b Study of Izokibep: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Hidradenitis Suppurativa Phase 2b Study of Izokibep (NCT05355805), a randomized phase 2 study. The primary outcome is Part B: Number of Participants Who Achieved HiSCR75 at Week 16.

2. Clinical Question

3. Trial Design

This is a Phase 2b study of izokibep in people with moderate to severe hidradenitis suppurativa. The registry lists randomized allocation and a parallel-group model, with an overall enrollment of 205. The study is marked completed. The recorded start date is 2022-05-05 and the primary completion date is 2023-08-02.

The study had an open-label Part A and a double-blind Part B. The posted primary outcome is from Part B, where participants were assigned to izokibep 160 mg every week, izokibep 160 mg every other week, or placebo on the corresponding schedule. The two placebo schedules transitioned to izokibep after the initial placebo period. Thus, the Week 16 endpoint concerns the initial comparison, rather than a comparison of continued placebo with izokibep throughout the entire study.

For the primary endpoint, the registry identifies the full analysis set in Part B as all participants randomized in Part B. The posted group sizes are 59 for placebo, 57 for weekly izokibep, and 59 for every-other-week izokibep. The registry also describes outcomes related to safety, immunogenicity, response thresholds, disease flares, lesion counts, and skin pain. Results are not posted for every listed secondary outcome in the registry record analyzed.

The registry does not report the original sample-size justification, detailed randomization procedures, the planned interim-analysis approach, or the complete statistical analysis plan. The posted results identify the endpoint population and the reported comparison method, but do not resolve those design details.

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: Part A was a single-arm, open-label, proof-of-concept investigation to explore preliminary efficacy and safety of izokibep. Once Part A was fully enrolled, subsequent participants were enrolled into Part B. Part B was a randomized, double-blind, placebo-controlled, parallel-group, dose-finding investigation to evaluate the efficacy, safety, and immunogenicity of izokibep in participants with moderate to severe hidradenitis suppurativa.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FAS, Part A: all participants who received at lease one dose of study drug in Part A.

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: Full Analysis Set (FAS), Part A: all participants who received at lease one dose of study drug in Part A. FAS, Part B: all participants randomized in Part B.

6. Primary Endpoint

The registry lists the primary outcome as Part B: Number of Participants Who Achieved HiSCR75 at Week 16, measured over Part B: Baseline to Week 16.

The primary endpoint counts participants in Part B who achieved HiSCR75 at Week 16. HiSCR75 is defined as at least a 75% reduction from baseline in the total abscess and inflammatory nodule count, with no increase from baseline in abscess or draining fistula count. The outcome therefore combines improvement in lesion counts with a condition preventing worsening in specified lesion types. It is a binary response: each participant either meets the definition at the assessment or does not.

Clinical trial endpoints often use a prespecified response threshold to turn a change in symptoms or signs into an interpretable participant-level outcome. In general, a binary endpoint can make it straightforward to compare the share of participants meeting a response definition between groups. The threshold also determines what counts as a response, so the result does not describe the full range of change in lesion counts or the experience of every participant.

The registry identifies the time frame as baseline to Week 16 and the analysis population as all participants randomized in Part B. It does not report in this record why HiSCR75 was selected over another response threshold, how missing Week 16 assessments were handled, or the detailed rules for deriving the endpoint when component measurements were unavailable. Those details are not reported in the registry record.

7. Results Posted in the Registry

• Part B Izokibep 160 mg QW: 36.8% (21/57) versus 27.1% (16/59) on control; risk difference 9.7 percentage points (95% CI -7.2 to 26.6), risk ratio 1.36 (0.79–2.33); unadjusted two-proportion z-test p = 0.261.
• Part B Izokibep 160 mg Q2W: 32.2% (19/59) versus 27.1% (16/59) on control; risk difference 5.1 percentage points (95% CI -11.4 to 21.5), risk ratio 1.19 (0.68–2.08); unadjusted two-proportion z-test p = 0.545.

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.

Part B: Number of Participants Who Achieved HiSCR90 at Week 16

• 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:
  • Part B Izokibep 160 mg QW: 26.3% (15/57) versus 15.3% (9/59) on control; risk difference 11.1 percentage points (95% CI -3.6 to 25.7), risk ratio 1.73 (0.82–3.62); unadjusted two-proportion z-test p = 0.141.
  • Part B Izokibep 160 mg Q2W: 20.3% (12/59) versus 15.3% (9/59) on control; risk difference 5.1 percentage points (95% CI -8.7 to 18.9), risk ratio 1.33 (0.61–2.92); unadjusted two-proportion z-test p = 0.470.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Part B Izokibep 160 mg QW 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 Part B Izokibep 160 mg Q2W and the control. The interval gives the range of effects that remain compatible with the data.

Part B: Number of Participants Who Achieved HiSCR100 at Week 16

• 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:
  • Part B Izokibep 160 mg QW: 26.3% (15/57) versus 11.9% (7/59) on control; risk difference 14.5 percentage points (95% CI 0.4 to 28.5), risk ratio 2.22 (0.98–5.04); unadjusted two-proportion z-test p = 0.047.
  • Part B Izokibep 160 mg Q2W: 18.6% (11/59) versus 11.9% (7/59) on control; risk difference 6.8 percentage points (95% CI -6.1 to 19.7), risk ratio 1.57 (0.65–3.77); unadjusted two-proportion z-test p = 0.306.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Part B Izokibep 160 mg QW 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 Part B Izokibep 160 mg Q2W and the control. The interval gives the range of effects that remain compatible with the data.

Part B: Number of Participants Who Achieved HiSCR50 at Week 16

• 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:
  • Part B Izokibep 160 mg QW: 45.6% (26/57) versus 37.3% (22/59) on control; risk difference 8.3 percentage points (95% CI -9.5 to 26.2), risk ratio 1.22 (0.79–1.89); unadjusted two-proportion z-test p = 0.363.
  • Part B Izokibep 160 mg Q2W: 44.1% (26/59) versus 37.3% (22/59) on control; risk difference 6.8 percentage points (95% CI -10.9 to 24.5), risk ratio 1.18 (0.76–1.83); unadjusted two-proportion z-test p = 0.453.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Part B Izokibep 160 mg QW 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 Part B Izokibep 160 mg Q2W and the control. The interval gives the range of effects that remain compatible with the data.

The listed secondary outcomes include more stringent and less stringent HiSCR response thresholds, disease flares, lesion outcomes, and a patient-reported skin-pain outcome. Among the secondary HiSCR endpoints with posted results, the point estimates generally favor the izokibep groups, but the corresponding recalculated intervals are mostly broad and include no difference. HiSCR100 for weekly izokibep is the exception in the unadjusted recalculation: its confidence interval is above zero, while the registry’s Cochran-Mantel-Haenszel p-value is 0.051. That contrast illustrates why the analysis method and multiplicity context matter, rather than establishing a definitive secondary finding.

Across the posted secondary response thresholds, results are not uniformly decisive, and the pattern should be read alongside the primary HiSCR75 comparison, whose unadjusted intervals include zero for both schedules. The secondary outcomes do not replace the primary endpoint or change its result. They may help describe response at alternative thresholds, but they also involve additional comparisons and should not be treated as independent confirmation of the primary result.

The registry lists 13 outcome measures and 14 analyses, while the registry entries identify 11 posted secondary outcomes. The full multiplicity plan is not reported in the registry record. Without knowing whether the outcomes were hierarchically ordered, designated exploratory, or adjusted for multiple testing, isolated secondary p-values carry less weight than a result from a clearly prespecified primary analysis. The registry also lists secondary outcomes for disease flares, lesion status, and skin pain; their results are not all included in the posted results analyzed here, so no conclusion about those outcomes can be drawn from the information available.

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

• Part A: Number of Participants With Treatment-emergent Adverse Events (TEAEs)
• Part A: Number of Participants Testing Positive for Anti-drug Antibodies (ADAs)
• Part B: Number of Participants Who Achieved HiSCR90 at Week 16
• Part B: Number of Participants Who Achieved HiSCR100 at Week 16
• Part B: Number of Participants Who Achieved HiSCR50 at Week 16
• Part B: Percentage of Participants Who Experienced ≥ 1 Disease Flare Through 16 Weeks of Treatment
• Part B: Number of Participants With Hurley Stage II at Baseline Who Achieved AN Count of 0, 1, or 2
• Part B: Number of Participants Who Achieved at Least a 3-Point Reduction From Baseline in Numeric Rating Scale (NRS) in Patient Global Assessment of Skin Pain at Its Worst at Week 16 Among Participants With Baseline NRS ≥ 4

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary: a participant either achieved HiSCR75 by Week 16 or did not. For this kind of outcome, a risk is the proportion of participants with the event—in this case, achieving the response—in a group. A risk difference subtracts the comparator group’s risk from the intervention group’s risk. A positive difference indicates a higher observed response risk in the intervention group; it does not by itself establish that the difference is statistically persuasive or clinically important.

The posted counts allow an unadjusted comparison of each izokibep group with placebo. For weekly izokibep, the recalculated risk difference is 0.097; for every-other-week izokibep it is 0.051. These estimates are expressed as proportions, and should not be read as participant counts. The recalculations use only the group counts and sizes, without incorporating any adjustment or stratification. They are not a replacement for the trial’s own analysis.

The registry reports that the sponsor used the Cochran-Mantel-Haenszel method for the two primary comparisons, with risk difference as the reported measure. This is a method for comparing categorical outcomes across groups, and it can account for strata when a stratified analysis is specified. The registry information analyzed does not identify the strata or provide the full model specification. The sponsor-reported risk differences are 8.27 and 4.19, with p-values of 0.305 and 0.619, respectively. The registry does not report confidence intervals for these results. Differences between a method based on stratified analysis and an unadjusted calculation can arise from the analysis details; the record does not provide enough detail to determine the exact reason for the numerical differences.

A confidence interval gives a range of effect estimates compatible with the observed data under the method’s assumptions. In repeated use of the same procedure, intervals constructed at a stated confidence level would cover the underlying value at that rate. The recalculated primary intervals include zero, the value corresponding to no risk difference. This means the data do not pin down the direction or size of the effect precisely. A confidence interval is not a guarantee that the true effect lies within the particular interval, nor does an interval crossing zero prove there is no effect.

A p-value summarizes the compatibility of the observed data with a specified null hypothesis and analysis model. Smaller p-values indicate greater tension with that null model, but a p-value does not measure effect magnitude, clinical importance, or the probability that the null hypothesis is true. The recalculated unadjusted p-values are 0.261 and 0.545. The sponsor-reported values are 0.305 and 0.619. They come from different analyses and should not be treated as though they were interchangeable estimates.

The study’s primary analysis population is described as all participants randomized in Part B. In general, analyzing randomized participants according to assigned group helps preserve the intended randomized comparison. The record does not report how missing endpoint observations were treated, whether every randomized participant contributed an observed Week 16 response, or whether sensitivity analyses assessed the effect of missing data. These omissions matter because the treatment of unavailable outcomes can affect a binary response comparison.

There are two primary comparisons against a shared placebo group, and multiple secondary endpoints and analyses are listed. When several outcomes or comparisons are examined, the chance of at least one apparently notable result can increase unless multiplicity is addressed. The registry record does not report whether a multiplicity procedure was planned or used. The secondary outcomes should therefore be read as supportive or exploratory unless their status and analysis plan are established from other reported trial documentation.

The posted planning illustrations use the observed effect as their starting point and consider smaller fractions of it. In general, over-dispersion is a concern when observed variability exceeds what a simple model assumes; for binary outcomes, differences in event rates and the chosen analysis can influence the precision and sample size required. The planning assumptions listed for these illustrations use a normal approximation and equal allocation. They are not evidence that the original trial was designed using those assumptions.

What does “recalculated” mean?

It refers to simple unadjusted calculations from the posted group counts and sizes. These estimates and p-values do not reproduce the sponsor’s Cochran-Mantel-Haenszel analysis. When interpreting the trial’s own inferential result, the sponsor-reported analysis is the relevant registry analysis; the recalculation is useful as a transparent check on the direction and approximate uncertainty implied by the summary counts.

Why distinguish the methods?

Different analysis methods can use different information and assumptions. An unadjusted comparison treats the groups as whole groups, while a Cochran-Mantel-Haenszel analysis can incorporate stratification. Without the complete statistical plan and specification, it is not possible to determine all methodological choices behind the sponsor’s estimates. Keeping the results distinct avoids attributing the recalculated confidence intervals or p-values to the sponsor.

11. Confidence Intervals and Precision

The recalculated Week 16 risk difference is 0.097 for weekly izokibep versus placebo, with a confidence interval from -0.072 to 0.266. For every-other-week izokibep versus placebo, it is 0.051, with a confidence interval from -0.114 to 0.215. Both intervals include zero. Thus, the posted counts do not estimate the direction of the difference with high precision, and they allow a range of possible effects that includes no difference.

The intervals are also broad relative to their point estimates. That breadth reflects uncertainty in the group comparison, including the limited number of participants and response events represented in the primary analysis. It would be misleading to focus only on the positive point estimates and ignore the range of effects compatible with the data. The estimates do not establish that the observed differences would be similar in another study.

The registry’s sponsor-reported primary analyses do not include confidence limits in the results used. Therefore, their precision cannot be assessed from a posted interval in this record. The recalculated intervals are unadjusted and are not substitutes for intervals from the sponsor’s analysis method. They should be interpreted as a separate illustration of uncertainty based on the posted counts.

Confidence intervals quantify statistical uncertainty under the method used; they do not address every source of uncertainty. They do not resolve concerns about missing outcomes, endpoint derivation, analysis choices, or the applicability of the results to people outside the study population. Such details are not fully reported in the registry record.

12. Planning a Similar Trial: Sample Size

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

The planning figures are expressed as participants per arm for these binary-outcome comparisons. The registry’s general sample-size assumptions state a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses a stated fraction of the observed effect as the effect to detect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the selected effect under those assumptions, if that effect were the true effect and the model assumptions held. The 90% power column gives the corresponding planning target for a 90% chance. These are design quantities, not claims about what happened in the completed trial. The figures are not the trial’s enrolled group sizes.

The calculations start from the observed effect and also consider planning for 75% and 50% of that observed effect. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller effect requires more participants per arm. The estimates can change substantially when the assumed effect changes. Because the observed effect itself is uncertain, planning directly from it should not be taken as a definitive future-trial recommendation.

These figures are planning illustrations, not observed power. Observed power calculated after a trial is complete largely restates the effect estimate and its uncertainty; it does not provide a separate measure of how convincing the result is. The original study’s design rationale, target effect, attrition allowance, and any other assumptions are not reported in the registry record.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.271; treatment proportion p₁ = 0.368; average p̄ = 0.320.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6596 = 1.2928.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6560 = 0.5521.
4. n = (1.2928 + 0.5521)² / (0.0972)² = 360.0, rounded up to 360 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 <- 0.271186440677966                          # control proportion
p1 <- 0.368421052631579                          # 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(5355805)
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 = 360 (80% power), 482 (90% power)
 75% of observed effect: n per arm = 628 (80% power), 840 (90% power)
 50% of observed effect: n per arm = 1,382 (80% power), 1,849 (90% power)
power.prop.test: 360 
Simulated power at n = 360 per arm: 0.806 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparisons using the Cochran-Mantel-Haenszel method and risk difference. For weekly izokibep versus placebo, the reported risk difference is 8.27 with p = 0.305. For every-other-week izokibep versus placebo, it is 4.19 with p = 0.619. The registry does not report confidence intervals for these analyses in the record.

The separate recalculations use the posted counts in unadjusted comparisons. They estimate risk differences of 0.097 and 0.051, with p-values of 0.261 and 0.545. Their confidence intervals are also available, but they belong to the recalculated analyses, not the sponsor’s reported analyses. The two sets of results should not be merged or selectively combined.

The registry record identifies the sponsor method but does not provide the full statistical specification, including the details needed to explain the numerical differences from the unadjusted calculations. Both sets of p-values are above 0.05, but the methods and reported risk-difference scales are not identical. The sponsor’s posted results are the trial’s own inferential analyses; the recalculations are a transparent, unadjusted check using summary counts. The record does not flag a discrepancy between them.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several treatment comparisons or outcomes. Each additional test creates another opportunity for a result to appear notable by chance, even if there is no underlying effect. A statistical plan can address this through approaches such as a prespecified testing sequence or adjustment to the decision criteria. This is a general methodological issue, not a claim that any particular procedure was used in this study.

The registry lists two izokibep schedules compared with a shared placebo group for the primary endpoint and describes numerous secondary outcomes. It reports 13 outcome measures and 14 analyses. The record does not report whether the primary comparisons were adjusted for multiplicity, whether a hierarchical testing sequence was used, or whether the secondary analyses were intended as confirmatory or exploratory. Accordingly, nominal p-values should not be interpreted as if the family of tests and the decision rules were known.

Missing outcome data can also affect a binary endpoint. If a participant’s Week 16 response is unavailable, the analysis must use a specified rule, such as a method for imputing or otherwise classifying the missing response. Different choices can yield different estimates, particularly when the amount or pattern of missingness differs between groups. The registry record does not report the number of missing primary outcomes, the handling rule, or sensitivity analyses examining alternative assumptions. The posted denominator counts alone do not establish that every randomized participant had an observed assessment.

The primary population is identified as the Part B full analysis set, described as all participants randomized in Part B. The registry record does not provide further detail about exclusions after randomization, protocol deviations, or analysis populations used for other outcomes. Nor does it report whether the primary model included any covariates or stratification factors beyond naming the Cochran-Mantel-Haenszel method. These omissions limit independent reconstruction of the sponsor’s analysis and assessment of how robust the result is to analytic choices.

These are reporting limitations, not evidence that the study did or did not use a particular method. The registry may not contain every detail from the complete protocol or statistical analysis plan. Based on the record, however, the multiplicity strategy and missing-data procedures are not reported in the registry record, so they cannot be assumed.

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: arthritis (4.2%), still's disease (4.2%), covid-19 pneumonia (3.8%), sepsis (3.3%), colonic abscess (3.3%).

The registry presents serious adverse events and other adverse events by study group and time period. In Part B through Week 16, serious adverse events affected 2 participants in the placebo group, 2 in the weekly izokibep group, and 1 in the every-other-week izokibep group. The corresponding group sizes at risk are 59, 57, and 59. The registry records no deaths in these groups. In Part A, 2 of 30 participants had a serious adverse event, and no deaths are recorded.

These are descriptive counts. They do not by themselves establish whether an event was caused by treatment, or whether the groups differ reliably in safety. Serious adverse events are distinct from the broader category of other adverse events; in the same Week 16 groups, the registry reports 25, 43, and 34 participants with other adverse events, respectively. The record also lists selected serious-event terms and percentages, but these do not provide enough context to infer comparative risks for individual events.

The later periods include participants who transitioned from placebo to izokibep, as well as participants continuing assigned izokibep schedules. Those periods should be read separately from the initial randomized comparison. Exposure time, event definitions, and detailed causal assessments are not reported in the information. The counts are not a complete safety assessment and should not be used to make treatment decisions.

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

The results describe how many participants in each Part B group met the registry’s HiSCR75 definition by Week 16. The observed counts and point estimates are higher in the two izokibep groups than in the placebo group. However, the recalculated confidence intervals include zero, and the sponsor-reported p-values do not provide strong evidence against a no-difference model. The data therefore leave considerable uncertainty about the size and direction of the underlying group differences.

This does not establish that the groups are identical. An interval that includes zero can reflect uncertainty that is too wide to distinguish no difference from effects in either direction. Conversely, a positive point estimate alone does not establish a real or clinically meaningful advantage. The record does not report a threshold for a clinically important difference, so statistical estimates cannot be translated into such a conclusion from these results alone.

The outcome is a specific response definition at a specific time point. It does not describe every change in disease activity, the longer-term comparison after placebo participants transitioned to izokibep, or each participant’s broader experience. Secondary endpoints may provide additional context, but there are multiple outcomes and the multiplicity plan is not reported. The missing-data procedures and complete analysis plan are also not reported, limiting assessment of the sensitivity of the results to those choices.

The posted results apply to the study population and randomized Part B groups described in the registry. They do not establish how the findings would apply to people outside that population, nor do they answer questions about long-term outcomes or comparative safety beyond the reported time periods. The statistical estimates are evidence about the recorded trial outcomes, not medical advice or a standalone basis for treatment decisions.

18. Why This Trial Matters Statistically

This trial is statistically informative because it reports a participant-level binary endpoint, group counts, group sizes, and both sponsor-reported and unadjusted comparison results. Readers can distinguish the observed response counts from estimates of between-group difference, and can see that the recalculated intervals are wide enough to include no difference. That distinction is central to interpreting trials: the observed direction of a point estimate is not the same as precise evidence about the size of an effect.

The study also highlights why analysis methods matter. The sponsor reports Cochran-Mantel-Haenszel comparisons, while the recalculations use unadjusted summary counts. Keeping those analyses separate avoids treating independently derived confidence intervals and p-values as if they were part of the sponsor’s model. It also makes the importance of complete reporting clear: without the full method specification, the exact source of numerical differences cannot be determined.

Finally, the multiple response thresholds and other secondary outcomes illustrate the challenge of interpreting a collection of results. A secondary finding can be useful for describing patterns, but its evidential weight depends on its prespecified role and how multiplicity was handled. Those details are not reported in the registry record. The trial therefore offers a useful case for examining effect estimates, precision, analysis populations, and reporting gaps together rather than relying on a single count or p-value.

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 registry record leaves several trial-specific uncertainties. The original sample-size rationale and target effect are not reported, so the planning illustrations based on observed effects cannot explain whether the completed trial was designed to answer the primary question with a particular precision. Randomization details, any stratification factors, and the complete primary analysis specification are also not reported.

The sponsor’s primary results lack confidence intervals in the record analyzed. The unadjusted recalculations give intervals, but they do not reproduce the sponsor’s Cochran-Mantel-Haenszel method. Because the full specification is unavailable, the reason for differences in the estimates cannot be established from the registry record alone. The reported RD values and recalculated risk differences are also presented on different numerical scales, so they should not be directly compared as if they were the same output.

Important information about missing primary outcome data is absent: the record does not state how many Week 16 outcomes were unavailable, how missing responses were handled, or whether sensitivity analyses were performed. The multiplicity strategy for the two primary comparisons and the numerous secondary outcomes is likewise not reported. These gaps limit interpretation of nominal p-values and confidence in the robustness of the results to analysis choices.

The posted safety counts are descriptive and split across different periods, including periods after placebo participants transitioned to izokibep. The available information does not provide complete exposure-adjusted comparisons or enough detail to attribute individual events to treatment. Finally, the results concern a defined Week 16 response threshold; they do not provide a complete account of other clinical outcomes or longer-term randomized comparisons.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Hidradenitis Suppurativa Phase 2b Study of Izokibep — NCT05355805.
• Registry record last updated 2025-06-03; status last verified 2025-03.
• Results first posted 2024-09-25.
• 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

NCT05355805 is a completed randomized Phase 2b study of izokibep in adults with moderate to severe hidradenitis suppurativa. It included an open-label Part A and a double-blind Part B. The primary Part B outcome was the number achieving HiSCR75 at Week 16, comparing weekly and every-other-week izokibep with placebo.

The sponsor-reported Cochran-Mantel-Haenszel analyses give risk differences of 8.27 and 4.19, with p-values of 0.305 and 0.619; confidence intervals are not reported for those analyses. Unadjusted recalculations from the posted counts give risk differences of 0.097 and 0.051, with confidence intervals that include zero. Multiple secondary outcomes and safety counts are listed, but details on multiplicity, missing-data handling, and the original sample-size rationale are not reported in the registry record.