Study of Guselkumab Versus Placebo for the Treatment of Low Body Surface Area Moderate Plaque Psoriasis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Guselkumab Versus Placebo for the Treatment of Low Body Surface Area Moderate Plaque Psoriasis (NCT06039189), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Achieved an Investigator's Global Assessment (IGA) Score of Cleared (0) or Minimal (1) at Week 16.

2. Clinical Question

The clinical question is focused on a defined assessment at a defined time, rather than on a broad measure of every aspect of psoriasis. The primary endpoint classifies each participant according to the final IGA score: participants either reached the specified cleared-or-minimal category or did not. The result is therefore a comparison of event percentages between groups.

The registry also lists secondary outcomes covering body surface area, PASI total score, IGA cleared status, and assessments of scalp, genital, and intertriginous involvement. The primary comparison does not by itself answer every question about those other measures or about outcomes beyond Week 16. Results for some secondary outcomes are posted, while numerical results for the other listed outcomes are not reported in the registry record.

3. Trial Design

The registry describes NCT06039189 as a phase 3b, multicenter, randomized, double-blind, placebo-controlled, parallel-group study. It enrolled 338 participants and is marked completed. The recorded start date is 2023-08-24, and the primary completion date is 2025-04-14. The sponsor is Janssen Research & Development, LLC.

Participants were assigned to guselkumab or placebo. The intervention descriptions specify subcutaneous injections, with placebo used as needed in the guselkumab group to maintain the blind. The arm descriptions also state that the placebo group would then receive guselkumab. The timing and details of that later treatment are not reported in the registry record, so the Week 16 comparison should be read using the group labels and endpoint results as posted rather than assuming unreported treatment details.

The primary analysis population is the full analysis set, described as all randomized participants. For the primary endpoint, the registry reports 113 participants in the placebo-followed-by-guselkumab group and 225 in the guselkumab group. The listed outcome is measured at Week 16 and is the percentage achieving IGA cleared (0) or minimal (1). The reported analysis uses a Cochran-Mantel-Haenszel method and presents an adjusted treatment difference.

The registry record does not report the original sample-size justification, the specific randomization stratification factors, or details of interim analyses. Those omissions limit what can be concluded about the design rationale and analysis procedures beyond the information stated in the 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS) included all participants who were randomized in 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.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Achieved an Investigator's Global Assessment (IGA) Score of Cleared (0) or Minimal (1) at Week 16, measured over Week 16.

The primary endpoint is the percentage of participants with an Investigator’s Global Assessment score of cleared (0) or minimal (1) at Week 16. IGA is a clinician assessment of plaque psoriasis based on induration, erythema, and scaling. Each feature is graded, and the final score classifies psoriasis from cleared through severe, with higher scores indicating greater severity.

This endpoint converts the assessment into a binary outcome for the main comparison: a participant either achieved the specified cleared-or-minimal category or did not. The resulting percentages can be compared between the randomized groups, and their difference expresses how much more frequently the endpoint occurred in one group than the other. The posted results give 12.4% for the placebo-followed-by-guselkumab group and 74.2% for the guselkumab group.

As a general statistical point, a binary endpoint can be clinically interpretable because it describes the proportion meeting a prespecified threshold. It also discards detail: participants with different scores outside the threshold are grouped together, and a score just inside the threshold is treated as an event just as a score farther into that category would be. The endpoint therefore answers the stated threshold question, not every question about the degree or distribution of change in the underlying assessment.

The Week 16 result is time-specific. It does not establish how the endpoint changes at other times, and the registry record does not report results beyond the time points listed for the posted outcomes.

7. Results Posted in the Registry

• Group 2: Guselkumab 100 mg: 74.2% (167/225) versus 12.4% (14/113) on control; risk difference 61.8 percentage points (95% CI 53.5 to 70.2), risk ratio 5.99 (3.65–9.84); 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.

Percent Change From Baseline in Body Surface Area (BSA) 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 deviations.
• Result:
  • Group 2: Guselkumab 100 mg: mean -80.50 versus -5.60 on control; difference -74.90 (95% CI -85.83 to -63.97), standardized effect d = -1.94; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Group 2: Guselkumab 100 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percent Change From Baseline in Psoriasis Area Severity Index (PASI) 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 deviations.
• Result:
  • Group 2: Guselkumab 100 mg: mean -82.60 versus -13.60 on control; difference -69.00 (95% CI -79.15 to -58.85), standardized effect d = -1.96; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Group 2: Guselkumab 100 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Who Achieved IGA Score of Cleared (0) 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:
  • Group 2: Guselkumab 100 mg: 40.4% (91/225) versus 3.5% (4/113) on control; risk difference 36.9 percentage points (95% CI 29.6 to 44.2), risk ratio 11.43 (4.31–30.30); 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 Group 2: Guselkumab 100 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The numerically posted secondary outcomes point in a direction broadly consistent with the primary result at Week 16. The posted BSA and PASI percent-change comparisons show more negative mean change in the guselkumab group than in the placebo-followed-by-guselkumab group. The IGA-cleared comparison also shows a higher event percentage in the guselkumab group. These outcomes use different measures of psoriasis status, so they complement the primary endpoint rather than duplicate it.

The registry lists additional secondary outcomes, including PASI response thresholds and assessments of scalp, genital, and intertriginous involvement. Numerical results for those outcomes are not reported in the registry record. The overall pattern should therefore be described only from the outcomes with posted numerical results; it cannot be extended to every endpoint listed in the registration.

Secondary findings generally carry less inferential weight than a designated primary result when many outcomes are examined. As a general statistical issue, evaluating many hypotheses increases the chance that at least one will appear statistically significant by chance if all are treated as independent confirmatory tests. The registry record does not report whether a multiplicity adjustment or hierarchical testing plan was used for secondary outcomes. Their p-values should therefore be read as reported, without assuming control of the overall false-positive risk.

These secondary measures add context to the Week 16 primary comparison, but they do not replace it. Nor do they establish a single combined measure of benefit or resolve the unreported results for other listed outcomes. The endpoint-specific definitions, analysis methods, and uncertainty remain relevant when interpreting each result.

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

• Percent Change From Baseline in Body Surface Area (BSA) at Week 16
• Percent Change From Baseline in Psoriasis Area Severity Index (PASI) Total Score at Week 16
• Percentage of Participants Who Achieved IGA Score of Cleared (0) at Week 16
• Percentage of Participants Who Achieved PASI 90 Response at Week 16
• Percentage of Participants Who Achieved PASI 100 Response at Week 16
• Percentage of Participants Who Achieved Scalp Specific (ss)-IGA Score of Absence of Disease (0) or Very Mild Disease (1) at Week 16 Among Randomized Participants With Ss-IGA Score >=3 at Baseline
• Percentage of Participants Who Achieved Static Physician's Global Assessment of Genitalia (sPGA-G) Score of 0 or 1 at Week 16 Among Randomized Participants With sPGA-G Score >=3 at Baseline
• Percentage of Participants Who Achieved Intertriginous IGA (i-IGA) Score of Clear (0) or Minimal (1) at Week 16 Among Randomized Participants With an i-IGA Score >=3 at Baseline

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either achieved IGA cleared or minimal at Week 16 or did not. The group percentages describe the frequency of that event. A risk difference compares the event percentages by subtracting one group’s probability from the other’s. In general, a positive risk difference means the event was more frequent in the group placed first in the comparison. The recalculated primary risk difference is 0.618. The sponsor reports an adjusted treatment difference of 61.8 percentage points.

What does the reported adjusted comparison mean?

The registry names the Cochran-Mantel-Haenszel method for the primary analysis. In general, this method combines comparisons across strata and can account for stratification factors when those factors are specified. The registry record does not report the factors used for this analysis, so the details of the adjustment cannot be independently described from the posted record. The reported adjusted estimate is 61.8, with a 95% confidence interval from 53.4 to 70.1, and p < 0.001.

The unadjusted recalculation uses the posted group counts and denominators to produce a simple comparison of proportions. It is not the same as the sponsor’s adjusted analysis. Adjustment can change an estimate because it incorporates the structure of the analysis, while the unadjusted calculation treats the summary data as a direct two-group comparison. The primary recalculation is 0.618, and its 95% interval is 0.535 to 0.702. The sponsor’s result is the appropriate reference for the trial’s own reported analysis.

How should p-values be read?

A p-value measures how incompatible the observed data are with a specified null model, assuming that model and the analysis assumptions hold. It is not the probability that the null hypothesis is true, and it is not a measure of the size or importance of an effect. The reported primary p-value is <0.001. That is evidence against a no-difference null model for the reported comparison, but it does not quantify the probability that a future study would produce the same estimate.

For continuous secondary outcomes, the registry reports mean changes and sponsor analyses using a Mixed Model Repeated Measures method. In general, repeated-measures models use information across repeated assessments and can estimate group differences while accounting for correlations among measurements from the same participant. The specific model terms, covariance structure, and missing-data assumptions are not reported in the registry record. The sponsor’s Week 16 estimates are least-squares mean differences, which are model-based comparisons rather than simple differences between the posted group means.

The recalculated continuous comparisons are unadjusted mean differences based on the posted summaries. For body surface area percent change, the recalculated difference is -74.9, with a 95% interval from -85.83 to -63.97; the sponsor-reported least-squares mean difference is -74.48, with a 95% interval from -83.33 to -65.62. For PASI percent change, the recalculated difference is -69.0, with a 95% interval from -79.15 to -58.85; the sponsor-reported least-squares mean difference is -68.96, with a 95% interval from -77.06 to -60.87. The negative signs indicate that the reported mean percent changes were lower in the guselkumab group on these change-from-baseline scales.

General statistical context: confidence intervals describe uncertainty around an estimate under the analysis model. Wider intervals indicate less precision; narrower intervals indicate more precision, all else equal. For binary outcomes, the number of events and the group denominators affect precision. For continuous outcomes, variability and sample size contribute to the uncertainty of a mean difference. These principles help explain the reported intervals but do not supply missing details about the trial’s own analysis plan.

Planning illustrations based on observed effects are different from the trial’s original design calculations. They show hypothetical participant requirements under stated assumptions and effect sizes; they do not establish what assumptions were used by the study team. The original sample-size rationale and detailed statistical plan are not reported in the registry record.

11. Confidence Intervals and Precision

The primary sponsor-reported 95% confidence interval for the adjusted treatment difference runs from 53.4 to 70.1 percentage points, around an estimate of 61.8 percentage points. The recalculated unadjusted risk difference has a 95% interval from 0.535 to 0.702. Both intervals lie above zero, indicating that the estimates are not compatible with no group difference at the corresponding confidence level under the respective analyses.

A confidence interval is a measure of statistical uncertainty, not a guarantee that the true effect lies inside that specific interval. In general, the interval procedure is designed to cover the underlying quantity at its stated confidence level over repeated use under its assumptions. The interval is useful for judging both the direction of the estimate and the range of effect sizes reasonably compatible with the data and method.

For the posted secondary outcomes, the intervals for the recalculated BSA and PASI mean differences are also entirely below zero. The sponsor’s model-based intervals for those outcomes are likewise below zero. For IGA cleared at Week 16, the sponsor-reported adjusted difference is 36.9 percentage points, with a 95% confidence interval from 29.6 to 44.1. These are distinct endpoints and analyses; their intervals should not be treated as interchangeable evidence or combined informally.

Precision depends on more than the point estimate. As a general principle, event counts, group sizes, variability, and analysis choices all affect interval width. The registry does not report all details needed to assess every source of uncertainty, including the full model specification and missing-data methods. The intervals describe sampling uncertainty under the reported analyses; they do not cover all uncertainty about generalizability, measurement, or unreported analytic choices.

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 planning figures are illustrations based on the observed effect, not the trial’s original sample-size justification. For these non-time-to-event outcomes, the figures are participants per arm, not a total across arms or a total number of events. The planning assumptions listed in the registry-derived analysis are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses the stated fraction of the observed effect as the effect to detect.

The 80% power column gives the hypothetical participants per arm associated with an 80% chance of detecting the specified effect under those assumptions, if the assumed effect and statistical model were correct. The 90% power column gives the corresponding planning count for a 90% chance. Greater planned power generally requires more participants, other assumptions being equal. The posted figures are very small for some observed-effect scenarios because the observed differences are large relative to the uncertainty in these data.

Rows describing 100% of the observed effect use the full observed effect as the target for the illustration. The 75% and 50% rows use progressively smaller target effects. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under the same assumptions. The figures are not evidence that a future study of that size would reproduce the observed result.

This is not observed power. The trial’s own original design assumptions, including its sample-size justification, are not reported in the registry record. The illustrations should be interpreted only as conditional planning calculations, not as a retrospective evaluation of whether the completed trial had adequate design power.

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 = 0.124; treatment proportion p₁ = 0.742; average p̄ = 0.433.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7007 = 1.3734.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5476 = 0.4609.
4. n = (1.3734 + 0.4609)² / (0.6183)² = 8.8, rounded up to 9 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 <- 0.123893805309735                          # control proportion
p1 <- 0.742222222222222                          # 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(6039189)
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 = 9 (80% power), 12 (90% power)
 75% of observed effect: n per arm = 16 (80% power), 21 (90% power)
 50% of observed effect: n per arm = 32 (80% power), 43 (90% power)
power.prop.test: 8.8 
Simulated power at n = 9 per arm: 0.816 (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 a sponsor analysis of the primary endpoint using the Cochran-Mantel-Haenszel method. Its adjusted treatment difference is 61.8 percentage points, with a 95% confidence interval from 53.4 to 70.1 and p < 0.001. The simple recalculation from the posted proportions gives a risk difference of 0.618, with a 95% interval from 0.535 to 0.702 and p < 0.001.

The figures are close, but they are not identical calculations: the sponsor’s estimate is adjusted, while the recalculation is an unadjusted comparison of the posted summaries. The registry record does not state the adjustment factors, preventing a full reconstruction of the sponsor’s method from the posted information. Because there is no flagged discrepancy, the recalculation serves as a transparent check on the summary data, not a replacement for the sponsor’s own analysis. The sponsor’s reported analysis takes precedence for the trial’s primary inference.

A similar distinction applies to the continuous secondary outcomes. Their recalculated mean differences are simple unadjusted comparisons, whereas the sponsor reports least-squares mean differences from Mixed Model Repeated Measures analyses. The estimates are close, but the model-based results remain the study’s reported analyses. Differences between estimates or intervals can arise from adjustment and model structure and should not automatically be interpreted as errors.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when statistical tests are conducted for several endpoints, time points, groups, or analyses. In general, the more tests considered, the greater the chance of obtaining at least one small p-value even when no real difference exists across the full set of hypotheses. Common approaches to this issue include adjusting significance thresholds or specifying a testing sequence, but the registry record does not report whether either approach was used.

The primary endpoint is clearly identified, and its reported analysis has p < 0.001. However, the record does not provide a detailed multiplicity plan for the secondary outcomes, nor does it state whether secondary endpoints were confirmatory or exploratory. The secondary p-values should therefore not be interpreted as if a family-wise error rate had necessarily been controlled. The record also does not report an interim-analysis plan.

Missing-data handling is another important part of interpretation. The primary population is described as the full analysis set, including all randomized participants, but that definition does not explain how missing Week 16 assessments were treated. The record does not report the imputation method, assumptions about missingness, or sensitivity analyses. The continuous-outcome record names a repeated-measures model, but its missing-data assumptions and full specification are not reported.

Different missing-data assumptions can affect estimated outcomes, especially if the chance of a missing assessment is related to a participant’s outcome. Without the analysis details, the posted results cannot be used to determine how robust the estimates are to alternative assumptions. This limitation does not negate the reported findings; it defines what can be assessed from the registry record.

The record also does not give enough detail to reconstruct every aspect of the primary adjustment, such as the stratification factors. The sponsor’s analysis is consequently best read as reported, with the simple recalculation serving only as an unadjusted check. More detailed statistical documentation is 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: cholelithiasis (1.0%), appendicitis (1.0%), pneumonia (0.9%), angina unstable (0.4%), cardiac failure congestive (0.4%).

The registry lists serious adverse events for three safety groups. The placebo group has 1 serious adverse event among 113 participants at risk; the placebo-followed-by-guselkumab group has 2 among 104 at risk; and the guselkumab group has 12 among 225 at risk. No deaths are listed in any of those groups. These are counts and denominators as posted, not adjusted comparisons.

The record also lists serious event terms with percentages: cholelithiasis, 1.0%; appendicitis, 1.0%; pneumonia, 0.9%; angina unstable, 0.4%; cardiac failure congestive, 0.4%; and coronary artery occlusion, 0.4%. The registry lists these as top serious terms, but the details available do not establish a causal relationship to study treatment.

Safety counts require context. The safety group labels and at-risk denominators differ from the primary efficacy comparison, so the safety figures should not be substituted for the primary endpoint denominators. The registry record does not provide a detailed account of event timing, exposure-adjusted rates, or a formal between-group safety analysis. These figures describe reported serious adverse events in the stated groups; they do not alone characterize all safety outcomes.

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

The primary result describes the Week 16 percentage of participants who met the IGA cleared-or-minimal threshold in each randomized group. The posted percentages were 12.4% for placebo followed by guselkumab and 74.2% for guselkumab. The sponsor-reported adjusted difference was 61.8 percentage points, with a 95% confidence interval from 53.4 to 70.1. This is a group-level comparison for a specific outcome and time point.

The result does not mean every participant in the guselkumab group achieved the endpoint, or that no participant in the comparator group did. It does not describe the result for an individual, and it does not summarize every aspect of psoriasis severity. The endpoint classifies participants at a threshold; it is not a direct description of the full range of clinical changes.

The result also does not establish what happens at other times, what would occur in populations not represented in the trial, or how the groups compare on outcomes whose numerical results are not posted. The registry lists additional secondary outcomes, but several of their numerical results are not reported in the registry record. A Week 16 finding should not be generalized to a longer duration without corresponding data.

Statistical evidence of a difference is not the same as a complete judgment about clinical importance. The registry record does not provide a minimally important difference threshold, and the confidence interval expresses statistical uncertainty rather than every kind of uncertainty relevant to interpretation. The findings should be read alongside endpoint definitions, analysis choices, and limitations in the posted record.

These data alone do not provide medical advice or establish what treatment choice is appropriate for any person. They report a comparative result from this trial and should not be treated as a guarantee of outcome or a complete account of benefits and risks.

18. Why This Trial Matters Statistically

This trial is statistically informative because it defines a specific population and tests a threshold-based clinical assessment at a specified time. The randomized, double-blind, parallel-group design provides a structured comparison between assigned groups, while the primary endpoint makes the result interpretable as the percentage reaching a stated IGA category.

The primary estimate is accompanied by a confidence interval and a reported p-value, allowing readers to consider both the magnitude and statistical precision of the group difference. The unadjusted recalculation provides a transparent check using the posted summary counts, while the sponsor’s adjusted analysis remains the appropriate reference for the trial’s reported inference. Keeping those analyses distinct illustrates why adjustment and model choice matter.

The secondary outcomes add a broader view through measures of body surface area, PASI, and other site-specific assessments. At the same time, the record illustrates why secondary results need careful framing: not every listed outcome has numerical results posted, and the multiplicity plan is not reported. Statistical interpretation depends not only on whether individual p-values are small, but also on how many comparisons were made and how they were planned.

The record also makes clear that a completed trial’s posted summary does not necessarily expose every design or analysis detail. Information about sample-size justification, missing-data methods, interim analyses, and some model specifications is not reported. These gaps do not erase the numerical findings, but they constrain independent assessment of design assumptions and robustness.

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 gives a limited account of the statistical plan. The original sample-size justification, interim-analysis procedures, multiplicity strategy, and missing-data methods are not reported. The factors used for the primary adjustment and the full specifications for the repeated-measures analyses are also not reported. These omissions prevent full reconstruction of the sponsor’s analyses from the registry summary.

The primary endpoint is a threshold-based IGA outcome assessed at Week 16. It does not convey the entire distribution of IGA scores or establish durability beyond the stated time point. The record identifies additional outcomes, but numerical results for several listed endpoints are not reported. As a result, the available numerical summary offers an incomplete picture of all outcomes named in the registration.

The group labels require care: the primary comparator is called “Placebo Followed by Guselkumab 100 mg,” while the arm description says placebo was followed by guselkumab. The registry record does not give the timing details needed to further characterize the later treatment in relation to the Week 16 assessment. Safety group labels also differ from the primary analysis labels and use different denominators.

The recalculated comparisons are unadjusted summaries, not replacements for the sponsor analyses. They cannot reproduce model-based or adjusted estimates without the relevant model and adjustment details. Finally, the registry summary alone cannot establish generalizability to people unlike the trial population or address outcomes that are not posted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Guselkumab Versus Placebo for the Treatment of Low Body Surface Area Moderate Plaque Psoriasis — NCT06039189.
• Registry record last updated 2026-05-01; status last verified 2026-04.
• Results first posted 2026-05-01.
• 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

NCT06039189 is a completed randomized, double-blind, parallel-group phase 3b study of guselkumab versus placebo for low body surface area moderate plaque psoriasis with special site involvement. The registry reports enrollment of 338 participants. The primary endpoint is the percentage achieving IGA cleared or minimal at Week 16 in the full analysis set.

The sponsor-reported adjusted difference was 61.8 percentage points, with a 95% confidence interval from 53.4 to 70.1 and p < 0.001. The posted group percentages were 12.4% for placebo followed by guselkumab and 74.2% for guselkumab. Numerical results are also posted for three secondary outcomes; several other listed secondary outcomes do not have numerical results reported in the registry record.

The registry record does not report the original sample-size justification, multiplicity plan, interim analyses, or missing-data methods. These details limit independent assessment of the design and analysis beyond the reported results.