A Study of LY3041658 in Adults With Hidradenitis Suppurativa: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of LY3041658 in Adults With Hidradenitis Suppurativa (NCT04493502), a randomized phase 2 study. The primary outcome is Percentage of Participants Achieving Hidradenitis Suppurativa Clinical Response (HiSCR) at Week 16.

2. Clinical Question

The primary question focuses on a defined clinical response rather than a change in a single symptom or lesion count. HiSCR requires a substantial reduction in the combined count of abscesses and inflammatory nodules, while also requiring that abscesses and draining fistulae do not increase from baseline. The endpoint therefore combines improvement in the overall lesion count with safeguards against worsening in two other lesion measures.

The comparison is between randomized groups in a phase 2 study. The registry lists 72 participants enrolled, while the primary outcome reports 22 participants in the placebo group and 45 in the LY3041658 group. The registry defines the primary population as participants who were randomized and received at least one dose. It does not report why the number in the outcome groups differs from total enrollment.

The central statistical issue is not only which group had the larger observed response percentage, but also how uncertain the estimated difference is. The confidence interval for the group comparison includes both no difference and possible differences in either direction. The posted result therefore needs to be read as an estimate with appreciable uncertainty, rather than as a definitive separation between treatments.

3. Trial Design

The study is listed as a completed, multicenter, randomized, double-blind, placebo-controlled phase 2 trial. Its official title describes a parallel-group design. The registry lists Eli Lilly and Company as the sponsor. The study start date is 2020-08-26, and the primary completion date is 2022-03-15. These dates describe the trial record; they do not by themselves indicate when results were analyzed or reported.

Participants were assigned to LY3041658 or placebo. In the active-treatment group, participants received 600 mg LY3041658 intravenously once every 2 weeks. Placebo was administered intravenously in the comparison group, with a planned switch to 600 mg LY3041658 after Week 16. The primary endpoint is measured at Week 16, during the period when the randomized comparison was placebo-controlled.

The registry records 72 participants enrolled. For the primary outcome, the reported group sizes are 22 for placebo and 45 for LY3041658, within the stated modified Intent-to-Treat population of randomized participants who received at least one dose. The reason these outcome group counts do not account for the full enrollment is not reported in the registry record. The record also does not report the original design assumptions used to choose the enrollment target, such as an anticipated treatment difference or a planned statistical power.

Two secondary outcomes are listed: change from baseline to Week 16 in the total number of abscesses and inflammatory nodules, and change from baseline to Week 16 in skin pain on the HS Numeric Rating Scale. The placebo-to-active-treatment switch after Week 16 means that these Week 16 outcomes address the randomized comparison before that planned switch. The registry record does not provide enough information to characterize later comparative outcomes as a continued placebo-controlled comparison.

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: Participants were randomized in a 2:1 ratio to receive either 600 milligram (mg) LY3041658, or placebo in the double blind period (16 weeks).

Double Blind Treatment (Week 0 - 16)

Reasons for not completing this period:

Open-label Extension (Week 16 - 36)

Reasons for not completing this period:

Post-treatment Follow-up (10 Weeks)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified Intent-to-Treat (mITT) Population: All randomized participants who received at least one dose of study drug.

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: All randomized participants who received at least one dose of study drug.

6. Primary Endpoint

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

The primary endpoint is the percentage of participants achieving HiSCR at Week 16. A participant meets the response definition if the total abscess and inflammatory nodule count is reduced by at least 50% from baseline, with no increase in abscess count and no increase in draining fistulae count. This is a binary outcome: each participant is classified as a responder or a non-responder for the endpoint.

A composite response definition can capture improvement across related features while preventing a reduction in one component from being treated as a response if other specified features worsen. In this trial, HiSCR combines the abscess and inflammatory nodule count for the reduction criterion and applies separate no-increase conditions for abscesses and draining fistulae. The endpoint is therefore more informative than a simple change in one lesion measure, but it compresses several underlying changes into one responder classification.

The registry specifies non-responder imputation for missing primary endpoint data: participants with missing data were considered non-responders. This approach assigns a defined outcome when Week 16 response status is unavailable, but the registry record does not report how many participants had missing data or the reasons for missingness. As a result, the extent to which this rule affected the reported response percentages cannot be determined from the record.

HiSCR is assessed in the modified Intent-to-Treat population, defined as randomized participants who received at least one dose of study drug. This identifies the population used for the posted primary outcome, but does not establish how participants who were randomized but did not receive a dose were handled in other analyses.

7. Results Posted in the Registry

• 600 mg LY3041658: 48.9% (22/45) versus 31.8% (7/22) on control; risk difference 17.1 percentage points (95% CI -7.3 to 41.4), risk ratio 1.54 (0.78–3.04); unadjusted two-proportion z-test p = 0.185.

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.

Mean Change From Baseline to Week 16 in Total Number of Abscesses and Inflammatory Nodules (AN) Count

• 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:
  • 600 mg LY3041658: mean -6.52 versus -1.85 on control; difference -4.67 (95% CI -8.57 to -0.77), standardized effect d = -0.61; z-test p = 0.019.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for 600 mg LY3041658 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Mean Change From Baseline to Week 16 in Skin Pain on the HS Numeric Rating Scale (NRS)

• 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:
  • 600 mg LY3041658: mean -1.78 versus -1.83 on control; difference 0.05 (95% CI -1.41 to 1.51), standardized effect d = 0.02; z-test p = 0.946.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 600 mg LY3041658 and the control. The interval gives the range of effects that remain compatible with the data.

The two posted secondary outcomes cover different aspects of hidradenitis suppurativa: the total number of abscesses and inflammatory nodules, and skin pain measured on the HS Numeric Rating Scale. The overall pattern is not uniform across these measures. The sponsor’s lesion-count analysis reports a group difference with an interval that does not include zero, while the pain analysis reports an estimate close to zero with an interval that includes differences in either direction.

This pattern does not directly resolve the primary HiSCR comparison. The primary endpoint classifies participants according to a composite response rule, while the lesion-count outcome measures average change in a count and the pain outcome measures average change on a rating scale. A group-level mean difference in lesion count is not the same estimand as the difference in the proportion meeting HiSCR. The pain outcome assesses a separate symptom and need not track either lesion counts or the composite response in the same way.

The secondary outcomes can add context by showing whether the observed pattern on the primary endpoint is accompanied by changes in related measures. They do not, by themselves, establish that the primary response difference is real or clinically important. The registry lists two secondary outcomes, but the record does not report a multiplicity adjustment or a testing hierarchy. When several outcomes are assessed, unadjusted p-values carry less weight because repeated testing can increase the chance of an apparently notable result. The secondary findings are therefore best treated as supportive or exploratory information, with their estimates and intervals given more attention than a threshold-based reading of any single p-value.

The registry record also does not state clinical-importance thresholds for these secondary scales, nor does it provide the complete analysis specifications. This limits the conclusions that can be drawn about the magnitude of the observed changes beyond their reported units and statistical uncertainty.

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

• Mean Change From Baseline to Week 16 in Total Number of Abscesses and Inflammatory Nodules (AN) Count
• Mean Change From Baseline to Week 16 in Skin Pain on the HS Numeric Rating Scale (NRS)

9. Statistical Interpretation

10. Statistical Methods Explained

How should the primary estimate be read?

The primary endpoint is binary because each participant is classified as either achieving HiSCR or not achieving it. The group percentages describe the proportion classified as responders in each arm. A risk difference expresses the difference between those two response proportions on the proportion scale. The posted estimate is 0.171. Its 95% confidence interval, from -0.073 to 0.414, represents a range of values compatible with the observed data under the method used to construct that interval.

A confidence interval is not a guarantee that the true value lies inside the particular interval, nor does it assign equal probability to every value in the interval. It communicates the precision of an estimate under the assumptions of the statistical procedure. When an interval for a difference includes zero, the data are compatible with no group difference as well as with differences in either direction. Here the interval is wide enough to include both a negative risk difference and a positive one, so the direction and size of the underlying difference remain uncertain.

The sponsor’s reported primary analysis used logistic regression and reports a mean difference of 17.1, a 95% confidence interval from -7.3 to 41.4, and p = 0.189. The displayed group response percentages and the re-calculated risk difference are straightforward descriptions of the posted group summaries; they are not a substitute for the sponsor’s regression model. Regression methods can incorporate model structure or covariates, but the registry record does not report which covariates, if any, were included in this analysis. The sponsor’s estimate and its uncertainty are therefore the relevant reported inferential result.

A p-value summarizes how unusual data at least as incompatible with a null hypothesis would be if that null hypothesis and the model assumptions held. It does not measure the probability that the null hypothesis is true, the probability that a result will replicate, or the clinical importance of an estimate. The reported p-value should be read together with the point estimate and confidence interval. A result with a p-value above a conventional threshold can still be compatible with potentially meaningful differences, particularly when the confidence interval is broad; it does not establish that the groups are equivalent.

Why distinguish a binary endpoint from a continuous endpoint?

For a binary endpoint, the analysis compares responder proportions. For the secondary count and pain outcomes, the registry reports least-squares means and standard errors, and the sponsor reports ANCOVA estimates for mean differences in final values. A mean difference describes the contrast between group averages on the scale of the outcome. The count outcome is measured in abscesses and inflammatory nodules; the pain outcome is measured in units on the HS Numeric Rating Scale.

Least-squares means are model-based averages, rather than necessarily being simple arithmetic averages of the raw observations. ANCOVA is a general approach that compares outcomes while accounting for baseline values and other model terms when specified. The registry identifies ANCOVA as the method for the secondary sponsor analyses, but does not report the full model specification or the covariates used. The reported adjusted estimates should therefore be interpreted as the sponsor’s model-based comparisons, without inferring details that are not stated.

For the count outcome, the sponsor’s ANCOVA analysis reports a mean difference of -4.67, a 95% confidence interval from -8.69 to -0.64, and p = 0.024. For the pain outcome, the corresponding estimate is 0.05, with a 95% confidence interval from -1.44 to 1.53 and p = 0.949. The registry also includes simple unadjusted re-calculations from posted summary statistics. Those re-calculations can be useful as a check on scale and direction, but they do not reproduce the sponsor’s adjustment. In particular, the summary-statistic re-calculations use approximations for the continuous outcomes and should not be mistaken for the ANCOVA models.

What does over-dispersion mean in general?

In general, over-dispersion occurs when the variability in count data is greater than expected under a simple statistical model. It can make standard errors too small if the model does not allow for the extra variability, which can in turn make intervals appear too narrow and tests too favorable. This is a general issue in count-data analysis, not a finding established by this registry record. The record does not report a specific over-dispersion assessment or model choice for the lesion-count outcome.

How should missing primary outcomes be handled?

The primary endpoint uses non-responder imputation: participants with missing data are treated as non-responders. This rule ensures that missing primary endpoint status is assigned to a defined category for the responder analysis. Its consequences depend in part on how much data are missing and why they are missing. Those details are not reported in the registry record, so it is not possible to assess how sensitive the primary result is to alternative assumptions about missing outcomes.

The analysis population is the modified Intent-to-Treat population, described as all randomized participants who received at least one dose. This is the registry’s stated population for the primary endpoint. The record does not report a full accounting of participants randomized, treated, and included in each analysis, or whether additional sensitivity analyses were conducted.

Why are the secondary p-values not definitive on their own?

When several outcomes are examined, the chance of observing at least one apparently unusual result can increase if each is assessed without accounting for the full set of comparisons. General methods for addressing multiplicity include adjusting significance thresholds or defining a prespecified testing sequence. Whether any such approach was used for these secondary outcomes is not reported in the registry record. Their p-values are therefore best read as outcome-specific results rather than as conclusive evidence across a family of tests.

11. Confidence Intervals and Precision

The primary response percentages are 31.8% for placebo and 48.9% for 600 mg LY3041658. The corresponding 95% confidence intervals are 12.4 to 51.3 for placebo and 34.3 to 63.5 for LY3041658. These intervals describe the uncertainty around each group’s response percentage. They should not be used alone to judge the difference between groups: the interval for the comparison directly addresses that question.

The estimated primary risk difference is 0.171, with a 95% confidence interval from -0.073 to 0.414. This interval is broad and crosses zero. It is compatible with a range that includes no difference, a negative difference, and a positive difference. The observed percentages favor the LY3041658 group, but the interval indicates that the estimated contrast is not precise enough to distinguish among those possibilities with confidence.

The sponsor’s logistic regression estimate is 17.1, with a 95% confidence interval from -7.3 to 41.4. This reported interval also includes zero. The sponsor’s analysis is the relevant model-based result; the re-calculated interval and p-value are unadjusted calculations from the posted summaries. The two approaches give a similar overall message of uncertainty, but they are not identical analyses.

Confidence intervals for the secondary outcomes also convey different degrees of precision on their respective scales. The sponsor’s interval for the lesion-count mean difference runs from -8.69 to -0.64, while the interval for the pain mean difference runs from -1.44 to 1.53. These intervals should be interpreted in the units of their outcome and with attention to the model used. Precision is not the same as clinical importance: the registry record does not provide a threshold for a clinically important change on either secondary scale.

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 participants per arm, not total events. The sample-size illustration uses the observed effect as a starting point and considers planning for 100%, 75%, and 50% of that observed effect. For each assumed effect size, it gives the participants per arm associated with 80% power and 90% power. The larger power target requires a larger planned sample for a given assumed effect, and planning for a smaller effect requires more participants.

These illustrations assume 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. Those assumptions describe the planning illustration, not the original trial design. The registry record does not report the trial’s own sample-size justification or original design assumptions.

Power is the probability, under a specified assumed effect and statistical model, of rejecting the null hypothesis when that effect is present. The 80% and 90% columns therefore describe different planning targets under the stated assumptions; they do not describe certainty that a result will be statistically significant. The illustrations are based on the observed effects in this trial, which are estimates and may not match the effect in another study.

This is not observed power. Observed power is not a useful substitute for reading the estimated effect and its confidence interval after a trial has been completed. These figures are prospective planning illustrations only. They show how the required number of participants can rise as the assumed effect becomes smaller, while leaving the trial’s actual randomized and analyzed group sizes unchanged.

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 = 0.318; treatment proportion p₁ = 0.489; average p̄ = 0.404.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6938 = 1.3599.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6832 = 0.5750.
4. n = (1.3599 + 0.5750)² / (0.1707)² = 128.5, rounded up to 129 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 <- 0.318181818181818                          # control proportion
p1 <- 0.488888888888889                          # 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(4493502)
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 = 129 (80% power), 172 (90% power)
 75% of observed effect: n per arm = 225 (80% power), 301 (90% power)
 50% of observed effect: n per arm = 496 (80% power), 664 (90% power)
power.prop.test: 128.5 
Simulated power at n = 129 per arm: 0.800 (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 for the primary endpoint and both secondary endpoints. For HiSCR at Week 16, the sponsor used logistic regression and reported a mean difference of 17.1, a 95% confidence interval from -7.3 to 41.4, and p = 0.189. A simple unadjusted re-calculation from the posted group summaries gives a risk difference of 0.171, a 95% confidence interval from -0.073 to 0.414, and p = 0.185. The numerical estimates are on different representations of the response difference, and the methods are not identical.

The re-calculation is a check based on the posted summary statistics. It does not reproduce the sponsor’s regression analysis or its model assumptions. The sponsor’s reported analysis is the inferential result to use when describing the trial’s own analysis. The registry does not report sufficient detail to reconstruct the regression model, including any covariates or other model specifications.

For the secondary outcomes, the sponsor reports ANCOVA analyses. The lesion-count mean difference is -4.67, with a 95% confidence interval from -8.69 to -0.64 and p = 0.024. The skin-pain mean difference is 0.05, with a 95% confidence interval from -1.44 to 1.53 and p = 0.949. The unadjusted re-calculations use posted summary statistics and are distinct from these ANCOVA results. There is no reported discrepancy flag for the analyses. Agreement or similarity between calculations should not be taken to mean that their underlying methods are interchangeable.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary endpoint and two secondary outcomes. It gives the primary endpoint’s response definition and states that missing primary data were treated as non-response. However, the registry record does not report whether the primary hypothesis was part of a broader testing hierarchy or whether the secondary outcomes were subject to multiplicity control. It also does not report a prespecified order for testing outcomes.

Multiplicity matters because each additional statistical test creates another opportunity for a result to look unusual by chance. General statistical approaches may control the overall chance of false-positive findings by adjusting thresholds or sequencing tests, but the registry record does not say whether such an approach was used. The secondary p-values should consequently be read as unadjusted outcome-specific evidence unless further analysis details are available. This limitation does not change the numerical estimates, but it affects how strongly a collection of findings can be interpreted together.

For missing data, the primary endpoint applies non-responder imputation. Participants with missing primary endpoint information are classified as non-responders. The registry does not report the number of missing outcomes, the timing or reasons for missingness, or sensitivity analyses under alternative missing-data assumptions. Without those details, the effect of the imputation rule on the group percentages and estimated contrast cannot be evaluated.

The primary analysis population is the modified Intent-to-Treat population, defined as randomized participants who received at least one dose of study drug. The registry lists 72 enrolled participants, while the primary outcome reports 22 in the placebo group and 45 in the LY3041658 group. The record does not explain the difference between those figures or provide a complete participant flow for the outcome analysis. The analysis populations for the secondary endpoints are not reported in the registry record.

The registry names logistic regression for the primary analysis and ANCOVA for the secondary analyses, but it does not report the full model specifications, covariates, or detailed assumptions. These omissions limit independent reconstruction of the sponsor analyses and assessment of how model choices affected the estimates.

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: post procedural infection (4.5%), aortic stenosis (4.5%), atrial fibrillation (2.0%), pneumonia (2.0%).

The registry lists serious adverse events and other adverse events separately for the double-blind treatment period, the open-label extension, and follow-up. During the double-blind treatment period, 0 of 45 participants in the LY3041658 group had a serious adverse event, compared with 2 of 22 participants in the placebo group. Other adverse events were reported for 10 of 45 participants in the LY3041658 group and 2 of 22 participants in the placebo group. No deaths were listed in either group.

In the open-label extension, 1 of 49 participants had a serious adverse event and 13 of 49 had other adverse events; no deaths were listed. During follow-up, 0 of 39 participants had a serious adverse event, 2 of 39 had other adverse events, and no deaths were listed. The registry also identifies post procedural infection and aortic stenosis at 4.5% each, and atrial fibrillation and pneumonia at 2.0% each, among the listed serious adverse-event terms.

These counts should be interpreted within their stated periods and denominators. The open-label extension and follow-up groups are not the same randomized comparison as the double-blind period, and the registry record does not provide enough detail to infer comparative risk across all periods. Safety counts describe events recorded in the trial; they do not establish whether an event was caused by study treatment. The record does not provide further context such as event-level timing or attribution in the details.

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

The posted primary data show a higher observed Week 16 HiSCR percentage in the LY3041658 group than in the placebo group. The estimated risk difference is positive, but its 95% confidence interval includes zero and spans values in both directions. The sponsor’s logistic regression analysis likewise reports an interval that includes zero. The statistical evidence therefore does not establish a precise difference between groups at Week 16, and it also does not establish that the treatments are equivalent.

The result is a comparison of groups in this trial, for the stated population, endpoint definition, and assessment time. It is not a guarantee about the response of any individual participant. The primary endpoint is a composite binary classification, and a response status does not describe every change in lesions, pain, or other aspects of the condition. The secondary outcomes provide additional measurements but do not all show the same pattern, and their interpretation is limited by the absence of reported multiplicity procedures and some analysis details.

The registry record describes a phase 2 study with 72 participants enrolled and reports primary outcome group sizes of 22 and 45. The precision of the comparison is reflected in its confidence interval, not simply in the overall enrollment figure. The registry does not report the original sample-size justification, the number of missing primary outcomes, or enough information to determine how the difference between enrollment and primary outcome counts arose.

These findings should not be treated as medical advice or as a conclusion about treatment choice. They describe the posted estimates and their uncertainty. The record also does not establish the long-term comparative effect of LY3041658 versus placebo: the placebo group was scheduled to switch to LY3041658 after Week 16. Conclusions should remain tied to the reported Week 16 randomized comparison and the analyses documented in the registry.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate needs to be read with its uncertainty. The observed HiSCR percentage was higher in the LY3041658 arm, but the confidence interval for the estimated difference includes zero and allows for a broad range of possible contrasts. Looking only at the two percentages would obscure that uncertainty; looking only at a p-value would also discard information about the direction and plausible magnitude of the estimate.

It also illustrates the distinction between statistical estimands. The primary endpoint is a responder proportion based on a composite definition, while the secondary outcomes assess average change in a lesion count and pain score. A result on one measure cannot be substituted for a result on another. The differing patterns across outcomes are a reminder that related measures may capture different aspects of a condition.

The registry identifies the primary population and missing-data rule, which are essential to understanding how the primary result was formed. At the same time, details about missing outcomes, multiplicity, analysis populations for secondary outcomes, model specifications, and the original sample-size justification are not reported in the registry record. Recognizing these boundaries is part of interpreting a trial accurately: a result can be described precisely without making claims that the available record cannot support.

Finally, planning calculations based on an observed effect are not a retrospective measure of whether the trial was adequately powered. They are illustrations of how different assumed effects and power targets translate into planned group sizes under stated assumptions. The trial’s actual design assumptions are not reported, so the planning examples should not be confused with evidence about the design decisions made for this study.

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.

Several trial-specific limitations affect interpretation of the posted results. The primary estimate comes from reported groups of 22 placebo participants and 45 LY3041658 participants. The registry’s total enrollment is 72, and the reason the primary outcome group counts do not account for that total is not reported in the registry record. The record defines the primary population as randomized participants who received at least one dose, but does not give a complete participant flow.

The primary comparison has a broad 95% confidence interval that includes zero. This limits precision about the size and direction of the group difference. The primary outcome also uses non-responder imputation for missing data, but the number of missing outcomes and reasons for missingness are not reported. Sensitivity of the result to other missing-data assumptions cannot be assessed from the registry information.

The registry does not report whether multiplicity was addressed across the primary and secondary outcomes. This is particularly relevant when interpreting secondary p-values as a group. The secondary analysis populations, full model specifications, and covariates used in the logistic regression and ANCOVA analyses are also not reported, limiting independent assessment of those analyses.

The placebo group was scheduled to switch to LY3041658 after Week 16. The primary and listed secondary outcomes are assessed at Week 16, so the record does not support a longer-term randomized comparison with continued placebo. The registry also does not report the original sample-size justification, an interim-analysis plan, or additional protocol details beyond those stated in the trial record. Their absence should not be filled in by assumptions about standard practice.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of LY3041658 in Adults With Hidradenitis Suppurativa — NCT04493502.
• Registry record last updated 2023-04-28; status last verified 2023-04-01.
• Results first posted 2023-04-28.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT04493502 is a completed, multicenter, randomized, double-blind, parallel-group, placebo-controlled phase 2 study of LY3041658 in adults with moderate-to-severe hidradenitis suppurativa. The registry lists Eli Lilly and Company as sponsor, 72 participants enrolled, a start date of 2020-08-26, and a primary completion date of 2022-03-15.

The primary endpoint was the percentage achieving HiSCR at Week 16, with missing primary data treated as non-response. The reported percentages were 31.8% for placebo and 48.9% for 600 mg LY3041658. The sponsor’s logistic regression estimate was 17.1, with a 95% confidence interval from -7.3 to 41.4 and p = 0.189. The interval includes zero, leaving substantial uncertainty about the group difference.

The two listed secondary outcomes were change in abscess and inflammatory nodule count and change in skin pain. The record also reports adverse-event counts across the double-blind treatment, open-label extension, and follow-up periods. Details on multiplicity, the original sample-size justification, missing-data frequency, and full model specifications are not reported in the registry record.