A Study to Evaluate the Efficacy and Safety of Bimekizumab in Study Participants With Moderate to Severe Hidradenitis Suppurativa: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Efficacy and Safety of Bimekizumab in Study Participants With Moderate to Severe Hidradenitis Suppurativa (NCT04242498), a randomized phase 3 study. The primary outcome is Percentage of Participants Achieving Clinical Response as Measured by Hidradenitis Suppurativa Clinical Response 50 (HiSCR50) at Week 16.

2. Clinical Question

This clinical question is framed around a binary response: each participant is classified as a responder or nonresponder according to the endpoint definition. The registry record describes how missing observations and certain events after randomization were handled in determining response status. In particular, systemic antibiotic rescue medication, or discontinuation of study treatment due to an adverse event or lack of efficacy, was treated as an intercurrent event; participants were considered nonresponders following such an event.

The posted results include placebo and two bimekizumab regimen groups, with separate sample sizes and response percentages. The registry record does not include primary endpoint results for the third listed bimekizumab dosing regimen. The clinical question addressed by the posted comparisons is therefore limited to the two reported regimens versus placebo, rather than every regimen described in the arm information.

3. Trial Design

This was a phase 3, randomized, double-blind, placebo-controlled, multicenter study with a parallel-group model. The registry record lists an enrollment of 509 participants and a completed status. The study evaluated efficacy and safety of bimekizumab among participants with moderate to severe hidradenitis suppurativa.

Random allocation is intended to create groups that are comparable on average at the start of a trial, though it cannot ensure that every measured or unmeasured characteristic is balanced. A parallel-group design assigns participants to a study group and compares outcomes between groups. The record describes quadruple masking. It does not identify the specific roles covered by that masking label or provide further detail about how masking was maintained.

The listed interventions were bimekizumab and placebo. Arm descriptions identify three bimekizumab dosing regimens and a placebo group. Participants assigned to the placebo group received placebo during the initial treatment period and bimekizumab during the maintenance treatment period. The posted primary endpoint comparisons, however, are between placebo and bimekizumab dosing regimen 1 or dosing regimen 2. The registry record does not report primary endpoint estimates for the third listed regimen.

The primary endpoint was the percentage of participants achieving HiSCR50 at Week 16. The registry describes the randomized set as the primary analysis population. The primary outcome results report the number of participants in each arm, the response percentage, and a 95% confidence interval for that percentage. They also include sponsor-reported logistic regression analyses comparing each reported bimekizumab regimen with placebo.

Several other outcomes were registered, including HiSCR75, flare, dermatology-related quality of life, skin pain, and adverse events. The registry record does not report the original trial’s sample-size justification or the full statistical plan. Details about allocation procedures, the exact masking roles, and the reason only two regimen comparisons appear in the posted primary outcome results are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Participant Flow refers to the Randomized Set (RS) and Maintenance Set (MS).

Only the first 6 of 7 groups are shown.

Initial Treatment Period: Week 0-16

Reasons for not completing this period:

Maintenance Treatment Period: Week 16-48

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The RS consisted of all study participants randomized into the study.

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: Baseline Characteristics refer to the RS which consisted of all study participants randomized into the study.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving Clinical Response as Measured by Hidradenitis Suppurativa Clinical Response 50 (HiSCR50) at Week 16, measured over Week 16.

HiSCR50 is a binary clinical response endpoint assessed at Week 16. The registry defines a response as at least a 50 percent reduction from baseline in the total abscess and inflammatory nodule count, with no increase from baseline in abscess count or draining tunnel count. A participant either meets the full definition or does not. The reported outcome is the percentage of participants classified as responders in each group.

This type of endpoint combines change in lesion burden with a condition intended to guard against worsening in specified lesion categories. It is used to summarize whether participants reach a prespecified response threshold, rather than to report only the average change in lesion count. In general, a threshold can make a result easier to interpret as a responder proportion, but it also means that people with changes close to the threshold can fall into different response categories despite similar underlying changes.

The registry record specifies how missing data were handled: intermittent missing observations were imputed using multiple imputation with a Markov Chain Monte Carlo method, followed by monotone regression for monotone missing data. Lesion counts were imputed and then converted to responder status. Participants who experienced an intercurrent event were treated as nonresponders after that event. The registry defines these events as receipt of systemic antibiotic rescue medication or discontinuation of study treatment due to an adverse event or lack of efficacy.

The displayed percentages do not account for model effects from the logistic regression analysis. The sponsor’s separate adjusted analysis reports odds ratios from logistic regression. These are not the same quantity as the simple arm-level response percentages: the percentages describe the observed responder proportions, while the regression estimates a modeled comparison.

7. Results Posted in the Registry

• BKZ Dosing Regimen 1: 53.5% (77/144) versus 32.4% (24/74) on control; risk difference 21.0 percentage points (95% CI 7.6 to 34.5), risk ratio 1.65 (1.15–2.37); unadjusted two-proportion z-test p = 0.003.
• BKZ Dosing Regimen 2: 51.9% (151/291) versus 32.4% (24/74) on control; risk difference 19.5 percentage points (95% CI 7.3 to 31.6), risk ratio 1.60 (1.13–2.26); unadjusted two-proportion z-test p = 0.003.

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 Participants Achieving Clinical Response as Measured by Hidradenitis Suppurativa Clinical Response 75 (HiSCR75) at Week 16

• 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:
  • BKZ Dosing Regimen 1: 34.0% (49/144) versus 16.2% (12/74) on control; risk difference 17.8 percentage points (95% CI 6.4 to 29.2), risk ratio 2.10 (1.19–3.69); unadjusted two-proportion z-test p = 0.006.
  • BKZ Dosing Regimen 2: 35.7% (104/291) versus 16.2% (12/74) on control; risk difference 19.5 percentage points (95% CI 9.5 to 29.6), risk ratio 2.20 (1.28–3.78); 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 BKZ Dosing Regimen 1 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 BKZ Dosing Regimen 2 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Flare by Week 16

• 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:
  • BKZ Dosing Regimen 1: 23.6% (34/144) versus 28.4% (21/74) on control; risk difference -4.8 percentage points (95% CI -17.2 to 7.6), risk ratio 0.83 (0.52–1.33); unadjusted two-proportion z-test p = 0.443.
  • BKZ Dosing Regimen 2: 28.9% (84/291) versus 28.4% (21/74) on control; risk difference 0.5 percentage points (95% CI -11.0 to 12.0), risk ratio 1.02 (0.68–1.52); unadjusted two-proportion z-test p = 0.934.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BKZ Dosing Regimen 1 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 BKZ Dosing Regimen 2 and the control. The interval gives the range of effects that remain compatible with the data.

Absolute Change From Baseline in Dermatology Life Quality Index (DLQI) Total Score at Week 16

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • BKZ Dosing Regimen 1: mean -4.70 versus -3.20 on control; difference -1.50 (95% CI -3.03 to 0.03), standardized effect d = -0.26; z-test p = 0.055.
  • BKZ Dosing Regimen 2: mean -4.60 versus -3.20 on control; difference -1.40 (95% CI -2.71 to -0.09), standardized effect d = -0.27; z-test p = 0.037.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BKZ Dosing Regimen 1 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 mean is statistically lower for BKZ Dosing Regimen 2 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registered secondary outcomes cover several different domains: a more stringent clinical response threshold, flare, dermatology-related quality of life, worst skin pain and skin pain response, and treatment-emergent adverse events, including serious events and events leading to withdrawal. This breadth is useful because the primary lesion-count response does not describe every patient-relevant or safety dimension assessed by the study.

The numerical secondary findings posted for response, flare, and quality-of-life outcomes do not all represent the same type of comparison. They use different definitions and measurement scales, and the registry reports both categorical outcomes and a continuous score. The overall pattern should therefore be considered across outcome types rather than reduced to one summary judgment. The primary HiSCR50 result is the trial’s designated primary outcome; secondary findings can add context but do not replace it.

Results for pain and the full set of adverse-event outcomes are identified among registered outcomes, but their numerical results are not present in the outcome summaries included in the registry record analyzed for these comparisons. The registry record does not report those results in the material summarized for these outcomes. It is not appropriate to infer their direction or size from the primary result.

Unadjusted secondary p-values, where available, generally carry less weight than a prespecified primary comparison because multiple outcomes and comparisons create more opportunities for chance findings. The registry record does not report a multiplicity procedure for the secondary outcomes or the broader analysis family. Without that information, secondary estimates can be treated as exploratory context, with attention to their confidence intervals, definitions, and consistency rather than as independent confirmatory claims.

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

• Percentage of Participants Achieving Clinical Response as Measured by Hidradenitis Suppurativa Clinical Response 75 (HiSCR75) at Week 16
• Percentage of Participants With Flare by Week 16
• Absolute Change From Baseline in Dermatology Life Quality Index (DLQI) Total Score at Week 16
• Absolute Change From Baseline in Worst Skin Pain Score at Week 16
• Percentage of Participants Achieving Skin Pain Response at Week 16
• Percentage of Participants With Treatment-emergent Adverse Events (TEAEs) During the Study
• Percentage of Participants With Serious Treatment-emergent Adverse Events During the Study
• Percentage of Participants With Treatment-emergent Adverse Events (TEAEs) Leading to Withdrawal From the Study

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: participants are classified as achieving HiSCR50 or not achieving it. The posted arm-level summaries give a percentage and 95% confidence interval for each group. A confidence interval expresses the uncertainty around an estimated quantity under the method used to calculate it. It is not a range that contains a known true value with certainty, and it does not account for every possible source of bias or model limitation.

What does a risk difference describe?

A risk difference is the difference between two event proportions, expressed on the probability scale. For this endpoint, it describes the absolute difference in the percentage responding between a bimekizumab regimen and placebo. The recalculated estimates use the posted summary counts and are unadjusted. They do not incorporate model covariates or reproduce the sponsor’s logistic regression analysis. The associated confidence intervals express uncertainty around these unadjusted differences.

The recalculated risk difference is useful because it gives an absolute contrast in response probabilities. It differs from a relative measure, such as a risk ratio, and from the odds ratio reported by the sponsor. These measures answer related but nonidentical questions and can differ in magnitude, especially when the outcome is not rare. The registry’s primary analysis description specifically notes that the percentages do not account for model effects from the logistic regression model.

What does logistic regression contribute?

The sponsor’s reported primary analyses use logistic regression and present odds ratios. Logistic regression is a method for modeling the probability of a binary outcome through its odds. The odds ratio compares modeled odds between groups. The registry provides an odds ratio, a 97.5% confidence interval, a p-value, and a superiority label for each of the two reported comparisons. The registry record does not describe the complete model specification, including any covariates or other adjustment details, so those details should not be inferred.

The reported confidence level for these modeled comparisons is 97.5%, whereas the arm-level response percentages have 95% confidence intervals. The intervals are tied to their respective quantities and methods, and they should not be directly substituted for one another. The p-values also belong to the sponsor’s reported model analysis; the unadjusted recalculated p-values are separate summaries based on posted counts.

How were missing observations handled?

The primary endpoint description specifies multiple imputation with a Markov Chain Monte Carlo method for intermittent missing data, followed by monotone regression for monotone missing data. Lesion counts were imputed before they were dichotomized into response status. Multiple imputation is a general approach that represents uncertainty in missing values by using more than one completed version of the data and then combines analysis results. The registry does not report the imputation model details, the number of imputed data sets, or diagnostic assessments, so these aspects are not reported in the registry record.

The registry also states that intercurrent events were treated as nonresponse after the event. The specified events were systemic antibiotic rescue medication or discontinuation of study treatment due to an adverse event or lack of efficacy. This rule defines how those events enter the endpoint calculation; it is not the same as assuming the event did not occur. The exact event counts used in the primary analysis are not reported in the registry record.

What is the analysis population?

The registry describes the randomized set as all study participants randomized into the study. This identifies the intended population for the primary outcome summary. The registry record does not give further detail on exclusions, the exact analysis population used for each reported model, or how all post-randomization events were handled outside the endpoint description. These details are not reported in the registry record.

What can the recalculations tell us?

Recalculated results are simple, unadjusted analyses derived from the posted summary statistics. They provide an independent descriptive check of contrasts on the risk-difference scale, but they cannot reconstruct a model-based result or account for participant-level data. The registry lists no discrepancy between the recalculated summaries and the reported results. That does not make the estimands identical: the sponsor reports adjusted odds ratios, while recalculated estimates use unadjusted risk differences.

General statistical interpretation should distinguish the estimated effect, its uncertainty, the chosen endpoint definition, and the analysis model. A small p-value alone does not communicate the size or precision of an effect. The absolute response percentages, model-based odds ratios, risk differences, confidence intervals, and missing-data rules each contribute different information to understanding the posted result.

11. Confidence Intervals and Precision

The arm-level HiSCR50 percentages have 95% confidence intervals: 21.4% to 42.9% for placebo, 45.4% to 62.1% for bimekizumab dosing regimen 1, and 46.1% to 57.8% for regimen 2. These intervals show that the observed response percentages are estimates with uncertainty. The interval for placebo is wider than either bimekizumab interval, while the regimen 2 interval is narrower than regimen 1’s; the arm sizes differ, and precision depends in part on the amount of information available.

The sponsor’s modeled odds-ratio estimates have 97.5% confidence intervals. For regimen 1 versus placebo, the reported estimate is 2.422 with an interval from 1.221 to 4.804. For regimen 2 versus placebo, it is 2.287 with an interval from 1.220 to 4.291. These intervals describe uncertainty in the modeled odds ratios, not in the raw percentages or risk differences.

The recalculated unadjusted risk differences also have 95% confidence intervals. Regimen 1 versus placebo has an estimate of 0.210 and an interval from 0.076 to 0.345; regimen 2 versus placebo has an estimate of 0.195 and an interval from 0.073 to 0.316. In general, intervals that exclude the null value indicate that the estimates are not compatible with that null at the corresponding interval level under the method used. The null value is 1 for odds ratios and 0 for risk differences.

Confidence intervals do not show the range of outcomes that individual participants might experience, and their width alone does not address systematic error, missing-data assumptions, or multiplicity. The different confidence levels and effect measures also matter: the sponsor’s intervals and the recalculated intervals are not interchangeable. The registry record does not report additional sensitivity analyses that would show how robust the estimates are to alternative assumptions.

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 illustrations translate an observed effect into hypothetical group sizes under stated planning assumptions. For these binary outcomes, the figures are participants per arm, not total events. The planning 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 at the stated fraction of the observed effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the number of participants per arm in a hypothetical design that would have an 80% chance of detecting the specified effect if the assumptions and effect were correct. The 90% power column gives the corresponding group size for a 90% chance. Higher target power generally requires more participants when the other assumptions are held constant. Planning for 75% or 50% of the observed effect requires more participants than planning for the full observed effect, because smaller effects are harder to distinguish from random variation.

These figures are planning illustrations based on the observed results, not a reconstruction of the trial’s enrollment plan. The observed effect may not be the effect that a future study should expect, and the planning assumptions may not match a particular study’s design. The illustrations are not observed power: they do not measure the probability that the completed trial was successful, nor do they change the interpretation of its observed estimates.

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 = 0.324; treatment proportion p₁ = 0.535; average p̄ = 0.430.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7000 = 1.3721.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6841 = 0.5757.
4. n = (1.3721 + 0.5757)² / (0.2104)² = 85.7, rounded up to 86 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 <- 0.324324324324324                          # control proportion
p1 <- 0.534722222222222                          # 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(4242498)
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 = 86 (80% power), 115 (90% power)
 75% of observed effect: n per arm = 151 (80% power), 201 (90% power)
 50% of observed effect: n per arm = 332 (80% power), 444 (90% power)
power.prop.test: 85.7 
Simulated power at n = 86 per arm: 0.811 (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 comparisons use logistic regression and report odds ratios with 97.5% confidence intervals and p-values. The registry reports an odds ratio of 2.422 for dosing regimen 1 versus placebo and 2.287 for dosing regimen 2 versus placebo. The corresponding p-values are 0.004 and 0.003.

The recalculated comparisons use risk differences based directly on posted response counts and group sizes. They are unadjusted and have 95% confidence intervals. Because an odds ratio and a risk difference use different scales, and because the sponsor’s regression analysis is not the same calculation as a summary-statistic reanalysis, the estimates should not be expected to match numerically. They provide complementary views rather than duplicate estimates.

The registry record does not report the complete logistic regression specification, so the adjustment details cannot be independently reproduced from the posted summaries. The recalculations are not a replacement for the sponsor’s analysis or a reanalysis of participant-level data. The record does not flag a discrepancy between the posted findings and recalculated summaries; interpretation should still keep the distinct estimands and methods clear.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint description includes a specific missing-data procedure. Intermittent missing data were imputed using a Markov Chain Monte Carlo method, followed by monotone regression for monotone missing data. The lesion counts were imputed and then converted to binary response status. The registry also specifies that participants were treated as nonresponders after an intercurrent event, defined as receipt of systemic antibiotic rescue medication or discontinuation of study treatment due to an adverse event or lack of efficacy.

These rules are important because endpoint status depends on more than the final observed lesion counts. Imputation uses assumptions about the unobserved data, and the nonresponder rule defines how specified events affect response classification. The registry record does not report the imputation model, the number of imputed data sets, detailed diagnostic checks, or sensitivity analyses under alternative assumptions. Those details are not reported in the registry record.

The record reports comparisons for two bimekizumab regimens against placebo and identifies the sponsor analyses as superiority analyses. It does not report how the primary comparisons were organized within a formal multiplicity strategy, whether any testing sequence or adjustment was used, or how the wider family of secondary outcomes was handled. These matters are not reported in the registry record. The 97.5% confidence intervals and p-values are posted for the sponsor’s primary logistic regression comparisons, but their presence alone does not specify a complete family-wise error control plan.

Multiplicity matters when a trial evaluates several regimens, endpoints, or comparisons: repeated testing can increase the chance that at least one result appears notable by chance. This general concern does not establish that a particular reported finding is false; it means the analysis plan and testing framework are needed to understand confirmatory claims. In the absence of reported details, the primary results can be interpreted as posted, while secondary comparisons should be regarded with appropriate caution.

The registry describes the primary analysis population as all randomized participants. It does not provide a full account of analysis-population derivations for every outcome or model. Any further population exclusions, handling of protocol deviations, or sensitivity analysis populations are not reported in the registry record.

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: abdominal pain (1.4%), appendicitis (1.4%), hidradenitis (0.8%), gastroenteritis (0.8%), depression (0.8%).

The posted safety figures list serious treatment-emergent adverse events by group, with both the number at risk and the number affected. In the initial placebo group, 0 of 74 participants had a serious event listed. For bimekizumab dosing regimen 1, 3 of 142 participants were affected; for regimen 2, 9 of 290 participants were affected. The record also lists groups corresponding to placebo followed by regimen 2 and several regimen sequences during maintenance, with serious-event counts of 2 of 69, 4 of 133, 3 of 130, and 4 of 131, respectively.

These groups reflect different treatment sequences and should not be combined casually into a single comparison. The registry record does not provide a time-adjusted analysis or details about exposure duration for these safety groups. Serious adverse events are distinct from all treatment-emergent adverse events: the listed counts for other events are separate and should not be interpreted as serious-event counts.

No deaths are listed for any of the posted groups. The registry also lists serious-event terms, including abdominal pain and appendicitis at 1.4% each, and hidradenitis, gastroenteritis, depression, and anal fissure at 0.8% each. These summaries describe events recorded in the study; they do not by themselves establish causality or compare the overall safety profiles of treatments.

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

The Week 16 primary results describe the proportion of participants meeting the trial’s HiSCR50 response definition in the placebo group and in two reported bimekizumab regimen groups. The sponsor’s adjusted logistic regression comparisons and the unadjusted recalculated risk differences provide different statistical summaries of those posted outcomes. Their confidence intervals communicate uncertainty, and neither estimate should be treated as an exact measure of an underlying effect.

The endpoint is specific: it requires a reduction in abscess and inflammatory nodule count and no increase in abscess or draining tunnel count. It also follows the registry’s rules for missing observations and intercurrent events. Consequently, the result means response as operationalized by this endpoint and analysis, not every possible definition of symptom change, disease control, or quality of life.

The findings do not provide a primary outcome estimate for the third listed bimekizumab regimen. Nor do the primary response results answer questions about pain, quality of life, long-term outcomes, or safety beyond the posted measures and time frames. Registered secondary outcomes broaden the questions studied, but missing or unreported numerical results cannot be inferred from the primary findings.

In general, statistical evidence should be interpreted alongside design, measurement, missing-data handling, and the uncertainty around estimates. Randomization and masking support a controlled comparison, but the registry record does not report every design or analysis detail needed for a complete independent assessment. The results describe what was posted for this trial and do not, on their own, establish how findings apply to people or settings outside the study.

The reported p-values are evidence relative to statistical models and hypotheses; they are not probabilities that a treatment works, nor do they describe the chance that the findings arose by chance in a simple literal sense. Confidence intervals and effect measures are needed to understand both scale and precision. No treatment recommendation follows from these statistics alone.

18. Why This Trial Matters Statistically

This study illustrates why a clinical trial result should be read on more than one statistical scale. The arm-level HiSCR50 percentages are directly interpretable as responder proportions, while risk differences express absolute contrasts and the sponsor’s logistic regression reports odds ratios. These measures are related, but each answers a different question. Keeping them distinct helps prevent a modeled relative measure from being mistaken for an absolute percentage-point change.

The record also makes clear that endpoint construction matters. HiSCR50 combines a response threshold with a no-increase condition for specified lesion counts. Missing counts are imputed before response status is assigned, and participants with specified intercurrent events are classified as nonresponders after those events. Those choices shape the estimand and are part of the meaning of the primary result.

Precision is another central issue. Estimates are accompanied by confidence intervals, and the groups differ in size. The interval widths help readers gauge how much uncertainty remains, while the different reported interval levels reflect different analyses. A p-value alone would not communicate either the size of a contrast or its precision.

The secondary outcomes show why multiplicity and outcome hierarchy deserve attention. Trials may assess several response thresholds, symptoms, quality-of-life measures, and safety outcomes. A prespecified primary endpoint anchors interpretation, while secondary findings provide additional context. If multiplicity procedures and the complete statistical plan are not reported, readers should avoid treating every secondary comparison as independently confirmatory.

Finally, planning illustrations based on an observed effect are distinct from the trial’s original design rationale. They can illustrate how smaller target effects call for larger hypothetical group sizes under stated assumptions, but they cannot recover the original planning process or measure the completed trial’s observed power.

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 registry record does not report the original sample-size justification, full statistical analysis plan, or complete logistic regression specification. As a result, the rationale for the enrollment target, model covariates, and the planned multiplicity strategy cannot be assessed from the posted information. The record describes the primary missing-data method but does not provide its implementation details or sensitivity analyses.

The posted primary endpoint results cover placebo and two bimekizumab dosing regimens, although three bimekizumab regimens appear in the arm descriptions. The primary results for the third regimen are not reported in the registry record. The available numerical secondary outcome summaries also cover only part of the registered outcome list; numerical results for all registered pain and adverse-event outcomes are not included in the outcome details analyzed.

The sample sizes in the primary outcome summaries vary across groups, and the safety results include distinct treatment-sequence groups. The record does not provide enough detail to reconstruct exposure-adjusted safety comparisons or to combine the sequence-specific groups into a single estimate. Serious-event counts are descriptive and do not establish causality.

The recalculated risk differences are based on aggregate counts and are unadjusted. They cannot account for participant-level covariates or reproduce the sponsor’s model. The sponsor’s model details are not fully reported, so its estimates cannot be independently reproduced from the posted summary alone. Finally, the record’s registered design and posted outcomes do not answer questions beyond the specified study population, Week 16 primary endpoint, and reported follow-up measures.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Efficacy and Safety of Bimekizumab in Study Participants With Moderate to Severe Hidradenitis Suppurativa — NCT04242498.
• Registry record last updated 2026-10-26; status last verified 2026-09.
• Results first posted 2024-12-05.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed, randomized, double-blind, placebo-controlled, multicenter phase 3 parallel-group study of bimekizumab in participants with moderate to severe hidradenitis suppurativa. Enrollment was 509. The primary outcome was the percentage achieving HiSCR50 at Week 16, assessed in the randomized set.

Posted primary results include placebo and two bimekizumab dosing regimens. Sponsor-reported logistic regression analyses compare each reported regimen with placebo; unadjusted recalculations provide risk differences from posted summary counts. Secondary outcomes cover response, flare, quality of life, pain, and safety. The registry describes missing-data and intercurrent-event handling for the primary endpoint, but the original sample-size justification, complete analysis plan, and multiplicity strategy are not reported in the registry record.