A Study of Ixekizumab (LY2439821) Compared to Guselkumab in Participants With Moderate-to-Severe Plaque Psoriasis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Ixekizumab (LY2439821) Compared to Guselkumab in Participants With Moderate-to-Severe Plaque Psoriasis (NCT03573323), a randomized phase 4 study. The primary outcome is Percentage of Participants Achieving 100% Improvement From Baseline in Psoriasis Area and Severity Index (PASI 100).

2. Clinical Question

Clinically, the question is framed around complete improvement on the PASI measure at a specified assessment. PASI combines the extent of psoriasis across anatomical regions with ratings of scaling, redness and plaque thickness. It is a structured outcome measure; the endpoint is not a direct measure of every aspect of a participant’s experience or health.

The trial is randomized and double-blind, which supports a planned comparison between the assigned treatment groups while reducing some opportunities for assignment-related differences and assessment bias. The posted Week 12 results describe the proportion meeting the response definition in each group. They do not, by themselves, establish what would happen for every individual or in populations beyond those enrolled.

3. Trial Design

The registry record describes a Phase 4, randomized, double-blind, parallel-group study comparing ixekizumab with guselkumab in participants with moderate-to-severe plaque psoriasis. Its official title describes a 24-week study. The primary outcome assessed in the posted results is PASI 100 at Week 12, so the outcome assessment occurs before the end point named in the study title.

The record reports enrollment of 1027 participants. The primary outcome groups contain 520 participants in the ixekizumab arm and 507 in the guselkumab arm. The population for the primary analysis is all randomized participants. Participants who did not meet clinical response criteria or had missing data at Week 12 were considered non-responders for the Non-Responder Imputation analysis.

Both study drugs are described as subcutaneous injections. The ixekizumab arm description includes a starting dose and induction-period administrations; the guselkumab description includes scheduled active and placebo injections. These arm descriptions are truncated in the registry record, so the complete administration schedules and the full treatment-period details are not reported in the registry record. The record also lists placebo as an intervention, with placebo injections described as helping maintain blinding.

The study is marked completed. The registry record identifies Eli Lilly and Company as the sponsor. It does not report further details about randomization procedures, allocation concealment, masking procedures, stratification factors, site-level methods, or the sample-size justification for the original trial design. Those details should not be inferred from the designation “randomized, double-blind, parallel-group.”

The primary comparison is between the two active-treatment groups. The reported percentages describe response at Week 12, while the study title’s 24-week duration indicates the broader study timeframe. The registry information available for these results does not establish how later treatment or follow-up affected the Week 12 endpoint.

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: The study consists of a combined blinded treatment (trt) period with a 24-week duration followed by a post treatment follow-up (PTFU) period with a minimum of a 12-week duration. The Induction Dosing Period (12 Weeks) and Extension Period (12 Weeks) were combined for analysis and referred to as the blinded treatment periods.

Blinded Treatment Period (Weeks 0-24)

Reasons for not completing this period:

Post-Treatment Follow Up (Weeks 25-36)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants. Participants who did not meet clinical response criteria or have missing data at Week 12 were considered as non-responders for the Non-Responder Imputation (NRI) analysis.

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.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving 100% Improvement From Baseline in Psoriasis Area and Severity Index (PASI 100), measured over Week 12.

The primary endpoint is the percentage of participants achieving 100% improvement from baseline in the Psoriasis Area and Severity Index at Week 12. The registry defines PASI as a combined assessment of the extent of body-surface involvement in the head, trunk, arms and legs, together with the severity of scaling, erythema and plaque induration or thickness in each region. The resulting score ranges from 0 for no psoriasis to 72 for the most severe disease.

PASI 100 response is defined as at least 100% improvement in the PASI score compared with baseline. This endpoint expresses a threshold response as a proportion of participants, rather than reporting only a group average score. It therefore makes the comparison interpretable as the share of each randomized group meeting the specified response criterion.

As a general statistical point, a binary response endpoint simplifies a range of possible changes into whether each participant crossed a defined threshold. This can be useful for a clear treatment-group comparison, but it also means that differences in improvement among participants who do not meet the threshold are not distinguished by the response percentage. The endpoint does not capture every dimension of disease burden or treatment experience.

For the primary analysis, the registry says participants with missing Week 12 data or without the required clinical response were counted as non-responders under Non-Responder Imputation. That rule is part of the interpretation: the posted response percentages reflect both the endpoint definition and the stated approach to missing outcome data.

7. Results Posted in the Registry

• Guselkumab: 24.9% (126/507) versus 41.3% (215/520) on control; risk difference -16.5 percentage points (95% CI -22.2 to -10.8), risk ratio 0.60 (0.50–0.72); unadjusted two-proportion z-test p = <0.001.

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 PASI 75

• 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:
  • Guselkumab: 5.1% (26/507) versus 22.9% (119/520) on control; risk difference -17.8 percentage points (95% CI -21.8 to -13.7), risk ratio 0.22 (0.15–0.34); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Guselkumab than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Achieving PASI 90

• 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:
  • Guselkumab: 7.9% (40/507) versus 21.0% (109/520) on control; risk difference -13.1 percentage points (95% CI -17.3 to -8.9), risk ratio 0.38 (0.27–0.53); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Guselkumab than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Achieving PASI 100

• 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:
  • Guselkumab: 1.4% (7/507) versus 6.7% (35/520) on control; risk difference -5.4 percentage points (95% CI -7.7 to -3.0), risk ratio 0.21 (0.09–0.46); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Guselkumab than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary results cover PASI response thresholds at earlier assessments. Across the secondary results with numerical comparisons in the registry record, the reported response proportions are higher in the ixekizumab arm than in the guselkumab arm, and the reported comparisons have p < 0.001. This broad direction is consistent with the primary Week 12 PASI 100 result, while the secondary endpoints assess different thresholds or assessment times.

The registry record lists eight secondary outcome results, but the detailed numerical information available for interpretation includes Week 2 PASI 75, Week 4 PASI 90 and Week 4 PASI 100. Other secondary outcome names are listed, but their result estimates are not reported in the registry record information. The pattern across the reported secondary findings should therefore not be treated as a complete account of all listed secondary outcomes.

Secondary results are generally less definitive when many outcomes, thresholds or assessment times are examined. As a general statistical issue, multiple testing increases the chance of finding at least one apparently notable result even when there is no corresponding effect. The registry record does not report whether a multiplicity adjustment, testing hierarchy or other control of the overall error rate was planned or used. The secondary p-values should therefore be interpreted as unadjusted evidence unless a multiplicity procedure is documented.

The consistency of direction across the reported secondary results can add context to the primary finding, but it does not replace the prespecified primary endpoint or resolve uncertainty about unreported outcomes. The registry record does not report enough detail to determine the status of every secondary test within a formal testing sequence.

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

• Percentage of Participants Achieving PASI 75
• Percentage of Participants Achieving PASI 90
• Percentage of Participants Achieving PASI 100
• Percentage of Participants Achieving PASI 90
• Percentage of Participants Achieving Static Physician Global Assessment (sPGA) (0)
• Percentage of Participants Achieving PASI 50
• Percentage of Participants Achieving PASI 100
• Percentage of Participants Achieving PASI 100

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either met the PASI 100 response definition at Week 12 or did not. The reported group percentages estimate the proportion of participants meeting that definition in each arm. A binary endpoint allows the treatment groups to be compared using response proportions, but it does not describe how much participants improved when they failed to cross the response threshold.

What does a confidence interval describe?

In general, a confidence interval represents the uncertainty associated with an estimate under a statistical procedure and its assumptions. A narrower interval indicates greater precision for that estimate; a wider interval indicates less precision. The 95% confidence intervals reported for the arm-level percentages quantify uncertainty around each response proportion. They do not show the range of individual responses, and they do not directly provide the confidence interval for the difference between the arms.

What is the reported sponsor test?

The registry identifies the sponsor’s primary comparison as a Cochran-Mantel-Haenszel analysis and reports p < 0.001, with the result classified as superiority. In general, this method compares groups while accounting for strata. The registry information for this result does not specify the strata used, the detailed model settings, or a sponsor-reported effect estimate and confidence interval. Those unreported details should not be inferred from the method name alone.

A p-value is evaluated relative to a null hypothesis and the assumptions of the analysis. It is not a measure of the probability that the observed effect is due to chance, nor does it tell how large or important an effect is. The reported p-value should therefore be read with the response percentages and with the limitations of the available effect estimate in mind.

What is the unadjusted re-calculation?

The posted summaries also support a simple unadjusted comparison of the binary response proportions. The resulting risk difference is -0.165 for guselkumab contrasted with ixekizumab, with a 95% confidence interval from -0.222 to -0.108 and p < 0.001. The sign follows the contrast order: the guselkumab response proportion is compared with the ixekizumab response proportion. This calculation uses the posted summary data and is not the sponsor’s Cochran-Mantel-Haenszel analysis. The registry record marks no discrepancy between the reported analysis and the recalculation.

As a general statistical concept, a risk difference expresses the contrast between two response proportions on the probability scale. Its confidence interval describes uncertainty in that contrast under the calculation used. The interval in this unadjusted calculation does not account for any stratification or adjustment that may be present in the sponsor analysis. It should not be treated as if it were the sponsor’s adjusted result.

How does missing-data handling enter the analysis?

The primary analysis uses all randomized participants as its stated population. The record says participants who did not meet the clinical response criteria or had missing data at Week 12 were counted as non-responders under Non-Responder Imputation. In general, this approach assigns a non-response outcome rather than estimating the missing response from observed data. It creates a defined analysis rule, but the resulting estimate relies on the choice to treat missing outcomes in this way.

The registry record does not report the amount or reasons for missing Week 12 data, nor does it report sensitivity analyses using alternative missing-data assumptions. It also does not report the handling of missing data for every secondary endpoint in the information available for these results. Missingness could affect interpretation if its extent or pattern differed meaningfully between groups; whether that occurred is not reported in the registry record.

What can and cannot be inferred from the analysis?

Randomization is intended to make assigned groups comparable on average, while blinding is intended to limit some influences of treatment knowledge. These design features strengthen the basis for a between-group comparison, but they do not make every statistical or measurement assumption unnecessary. The registry record does not provide enough detail to assess randomization implementation, the strata for the sponsor’s test, or the full analysis plan.

The result supports a statement about the recorded Week 12 response proportions and the sponsor’s reported test. It does not, by itself, answer questions about durability, outcomes outside PASI 100, or effects in specific subgroups. As a general principle, a statistically detectable difference and a clinically meaningful difference are separate questions; the registry record does not report a threshold for clinical importance for this contrast.

11. Confidence Intervals and Precision

The primary arm-level estimates are reported with 95% confidence intervals: 41.3% (37.1% to 45.6%) for ixekizumab and 24.9% (21.1% to 28.6%) for guselkumab. The intervals convey uncertainty about the corresponding response percentages under the reported analysis. They do not mean that the true response rate has a 95% probability of lying inside the particular interval after the data have been observed.

The unadjusted re-calculation reports a risk difference of -0.165, with a 95% confidence interval from -0.222 to -0.108. Because this interval lies on the negative side of zero for the stated guselkumab-minus-ixekizumab contrast, it is consistent with a lower response proportion in the guselkumab group in this unadjusted comparison. The sponsor’s reported analysis is different in method and does not include a reported effect estimate or confidence interval in the registry record.

As a general statistical point, precision depends on the amount of information in the data and the variability of the outcome. Confidence intervals help readers judge how much uncertainty remains around an estimate, but do not address every possible source of bias or uncertainty. A narrow interval cannot correct for missing-data assumptions, outcome-measure limitations, or a mismatch between the study population and a different target population.

The intervals should be read as estimates rather than as guarantees about future studies. Another study may produce a different estimate, and the registry record does not report a replication or external validation of this comparison. The observed precision is tied to this study’s participants, endpoint definition, assessment time and analysis approach.

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 are planning calculations based on the observed effect, not the trial’s original design justification. For these binary outcomes, the listed figures are participants per arm, not a total across both arms. 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 to the stated fraction of the observed effect.

The 80% power column gives the illustrated number of participants per arm for a design with an 80% chance of detecting the specified effect under the planning assumptions, if that effect and those assumptions were correct. The 90% power column gives the corresponding per-arm number for a design with a 90% chance. Power describes a proposed design’s operating characteristics under assumptions; it is not a guarantee that a study will produce a statistically significant result.

The rows show planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. Smaller effects are harder to detect and therefore require more participants under the same assumptions. The table and curve are illustrations of how the planning requirement changes with the chosen effect and power target. They are not the enrollment plan used to conduct this trial, because the trial’s own original design assumptions and sample-size justification are not reported in the registry record.

This is not observed power. Observed power is not an additional interpretation of the trial’s result; the displayed planning figures instead describe hypothetical future designs using the stated assumptions. The figures should not be read as proof that the current trial was adequately or inadequately designed.

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 = 0.413; treatment proportion p₁ = 0.249; average p̄ = 0.331.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6655 = 1.3043.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6552 = 0.5514.
4. n = (1.3043 + 0.5514)² / (-0.1649)² = 126.6, rounded up to 127 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 <- 0.413461538461538                          # control proportion
p1 <- 0.248520710059172                          # 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(3573323)
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 = 127 (80% power), 169 (90% power)
 75% of observed effect: n per arm = 233 (80% power), 311 (90% power)
 50% of observed effect: n per arm = 539 (80% power), 720 (90% power)
power.prop.test: 126.6 
Simulated power at n = 127 per arm: 0.804 (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 reported primary analysis uses the Cochran-Mantel-Haenszel method and reports a superiority result with p < 0.001. The registry record does not give the sponsor’s numerical effect estimate or confidence interval for that analysis. The primary outcome summaries report 41.3% response in the ixekizumab arm and 24.9% in the guselkumab arm, each with a 95% confidence interval.

The unadjusted re-calculation from posted summary data gives a risk difference of -0.165 for guselkumab contrasted with ixekizumab, with a 95% confidence interval from -0.222 to -0.108 and p < 0.001. This calculation is not the sponsor’s stratified analysis and should not be presented as its estimate. The registry record marks no discrepancy, and the two results are aligned in the direction indicated by the observed response proportions and in the reported evidence against the null comparison.

The sponsor’s analysis is the registry’s reported inferential test; the re-calculation is useful as a transparent, unadjusted comparison based on group summaries. They answer closely related but not identical statistical questions because their methods differ. Details needed to reproduce or fully assess the sponsor’s adjustment are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The primary analysis population is described as all randomized participants. For the primary Week 12 endpoint, participants who did not meet clinical response criteria or had missing data were considered non-responders under Non-Responder Imputation. This makes the primary missing-outcome rule explicit, but the extent and reasons for missing data are not reported in the registry record for this result.

The record lists multiple secondary outcomes and reports results for several of them. When multiple endpoints, response thresholds or assessment times are tested, the chance of at least one small p-value can increase. As a general statistical principle, multiplicity procedures can control that risk by adjusting tests or specifying an order for interpretation. Whether any such procedure was planned or applied is not reported in the registry record. Consequently, the secondary results should not be interpreted as though family-wise error control or a hierarchical testing plan had been established.

The registry record does not report the original statistical analysis plan, detailed prespecification of each comparison, or the handling of missing data for all secondary endpoints. It also does not report sensitivity analyses that examine whether the primary result changes under alternative assumptions about missing Week 12 outcomes. These gaps limit assessment of robustness but do not alter the outcome definition and primary imputation rule that are reported.

As a general matter, treating missing outcomes as non-response can be reasonable for a response endpoint, but it is an assumption about how unobserved outcomes are classified. If missingness differs across arms or is related to response, different assumptions may yield different estimates. The record does not provide the missingness details needed to evaluate that possibility. These are limits on what can be established from the registry record, not evidence that the reported analysis is necessarily biased.

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: endometrial cancer stage iv (0.5%), myocardial infarction (0.4%), cellulitis (0.4%), syncope (0.4%), benign prostatic hyperplasia (0.3%).

The safety record lists serious adverse events among 519 participants at risk in the ixekizumab group, with 18 affected, and among 506 participants at risk in the guselkumab group, with 16 affected. In post-treatment follow-up, it lists 4 affected among 465 at risk for ixekizumab and 4 among 456 at risk for guselkumab. The record lists zero deaths in each of these groups.

These are counts within the groups recorded as at risk; they are not estimates of a causal treatment effect. The registry record does not provide a comparison analysis, confidence intervals, or a complete account of event timing and attribution alongside these counts. The listed serious-event terms include endometrial cancer stage iv, myocardial infarction, cellulitis, syncope, benign prostatic hyperplasia and ventricular tachycardia, each with the percentages stated in the registry record. Those listed terms should not be assumed to be exhaustive or interpreted as necessarily caused by study treatment.

Safety counts require context about definitions, exposure time, event ascertainment and follow-up. Those details are not reported in the registry record information available for this summary. The counts alone cannot establish whether one treatment is safer, and they do not support medical advice.

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

The primary result describes a difference in the observed proportion of randomized participants meeting the PASI 100 definition at Week 12. The ixekizumab arm’s reported response percentage is 41.3%, compared with 24.9% in the guselkumab arm. The sponsor reports a Cochran-Mantel-Haenszel superiority test with p < 0.001. The unadjusted re-calculation also reports a contrast in the direction of a lower response proportion for guselkumab relative to ixekizumab.

This finding applies to the defined outcome, population, assessment time and analysis rule. It does not show that every participant in one group had a better outcome than every participant in the other. It does not imply that every participant who failed to meet PASI 100 had no improvement. It also does not describe changes in outcomes not measured by PASI 100.

A statistically significant comparison is not the same as proof of clinical importance. The registry record does not report a threshold for what difference in PASI 100 response would be considered clinically important. The effect estimate and its confidence interval describe the size and precision of the statistical contrast, but interpretation of practical importance requires context beyond the p-value.

The result does not establish the duration of response after Week 12, because those conclusions are not reported for this primary endpoint. It also does not establish that the same response pattern would occur in populations with different characteristics, in other settings, or under different treatment schedules. The full treatment schedules are not completely available in the arm descriptions.

The safety counts are separate from the efficacy endpoint and should be interpreted on their own terms. The number of serious adverse events recorded in each group does not alone determine comparative safety, and the registry information does not include a complete comparative safety analysis in this summary. The efficacy result should not be translated into an individual treatment recommendation.

Overall, the registry record supports a statistical description of the Week 12 PASI 100 comparison and its reported uncertainty. Further claims about clinical importance, persistence, subgroup effects, other outcomes or comparative safety go beyond what is reported.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read at several levels. The group percentages describe the observed response proportions; the confidence intervals communicate uncertainty around estimates; and the sponsor’s test addresses a statistical comparison under its chosen method. These quantities are related, but they do not answer the same question. A p-value alone cannot replace an effect estimate or a description of precision.

The contrast also shows why the analysis method matters. The sponsor reports a Cochran-Mantel-Haenszel test, while the re-calculation is unadjusted and uses the posted group summaries. Both point in the same direction, but they are not interchangeable. The registry record does not provide the strata or full model details needed to reconstruct the sponsor’s reported analysis.

Missing-data handling is another central statistical choice. The primary analysis counts missing Week 12 observations as non-response, which makes the primary rule understandable and reproducible in principle. Yet the registry record does not report the amount or pattern of missingness or sensitivity analyses. Readers can identify the stated assumption without mistaking it for proof that missing data have no influence.

Finally, the secondary outcomes and sample-size illustrations serve different purposes. Secondary results can add context but may be affected by multiple testing, for which a correction or hierarchy is not reported. Planning illustrations show how hypothetical participant requirements change with assumptions about effect size and power; they do not reveal the trial’s original design rationale or its observed power. Keeping these distinctions clear helps prevent statistical evidence from being overstated.

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 information available for the primary result leaves several study-specific details unreported. The original sample-size justification and design assumptions are not reported, so the planning illustrations based on the observed effect cannot explain the trial’s enrollment target. The complete dosing descriptions are truncated, which limits description of the treatment schedules from this record alone.

The sponsor’s primary analysis is identified as Cochran-Mantel-Haenszel, but the strata, detailed model settings, effect estimate and confidence interval are not reported. The unadjusted re-calculation therefore offers a distinct summary comparison, not a reconstruction of the sponsor’s analysis. The record does not report enough detail to assess how adjustment might affect the estimate.

For missing data, the primary Week 12 approach is stated, but the amount and reasons for missing outcomes are not reported. Sensitivity analyses under alternative assumptions are also not reported. Missing-data handling for the secondary outcomes is not fully described in the registry information available for these results.

Several secondary outcomes are listed, while the detailed numerical results cover only some of them. The record does not report a multiplicity procedure or testing hierarchy. This limits how strongly the collection of secondary findings can be interpreted as confirmatory evidence.

The safety information provides event counts and selected serious-event terms but does not include a complete comparative analysis in the information summarized. Event timing, attribution and other details needed to interpret differences are not reported in the registry record. These limits mean the counts should be treated descriptively rather than as a definitive comparison of harms.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Ixekizumab (LY2439821) Compared to Guselkumab in Participants With Moderate-to-Severe Plaque Psoriasis — NCT03573323.
• Registry record last updated 2020-07-28; status last verified 2020-02.
• Results first posted 2020-07-28.
• 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

NCT03573323 is a completed, Phase 4, randomized, double-blind, parallel-group study sponsored by Eli Lilly and Company. It enrolled 1027 participants with moderate-to-severe plaque psoriasis and compared ixekizumab with guselkumab. The primary outcome was the percentage achieving PASI 100 at Week 12, with missing or non-responding participants classified as non-responders under Non-Responder Imputation.

The reported response proportions were 41.3% for ixekizumab and 24.9% for guselkumab. The sponsor’s Cochran-Mantel-Haenszel superiority analysis reported p < 0.001. An unadjusted re-calculation from the posted summaries gives a risk difference of -0.165 for guselkumab relative to ixekizumab, with a 95% confidence interval from -0.222 to -0.108.

The registry record does not report the original sample-size justification, a multiplicity procedure, or sensitivity analyses for missing data. The secondary results and safety counts provide additional context but have limits described in the record.