A Study of Safety and Effectiveness of Ustekinumab (CNTO 1275) in Patients With Moderate to Severe Plaque-type Psoriasis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Safety and Effectiveness of Ustekinumab (CNTO 1275) in Patients With Moderate to Severe Plaque-type Psoriasis (NCT00267969), a randomized phase 3 study. The primary outcome is Psoriasis Area-and-severity Index (PASI) 75% Improvement From Baseline at Week 12..

2. Clinical Question

The trial was designed to evaluate safety and effectiveness in moderate to severe plaque-type psoriasis. The record also lists a Week 12 Physician Global Assessment outcome, a Week 12 change in Dermatology Life Quality Index, and PASI 75 response at Week 52 as secondary outcomes. These address additional aspects of clinical status and later response, but they do not replace the primary Week 12 question. The placebo crossover and later response-guided treatment are important when interpreting results beyond the initial comparison: subsequent outcomes arise under a treatment history that differs from the original placebo-controlled period.

3. Trial Design

The registry identifies this as a phase 3, randomized, double-blind, parallel-group, placebo-controlled trial. Enrollment was 766, and the status is completed. The condition is psoriasis. The record gives a start of 2005-12 and primary completion of 2006-07. The sponsor is Centocor Research & Development, Inc.

Three groups are reported for the primary Week 12 endpoint: placebo, ustekinumab 45 mg, and ustekinumab 90 mg. The posted analysis counts 255 participants in the placebo group, 255 in the 45 mg group, and 256 in the 90 mg group. The active groups received treatment at Weeks 0, 4 and 16. The placebo group received placebo at Weeks 0 and 4, then crossed over to ustekinumab 45 mg or 90 mg at Weeks 12 and 16. Because the primary endpoint is assessed at Week 12, the reported Week 12 comparison is the relevant initial placebo-controlled assessment.

Treatment after Week 16 depended on clinical response. At Week 40, participants who achieved PASI 75 at both Week 28 and Week 40 were re-randomized either to withdraw from therapy or to continue maintenance treatment every 12 weeks at their assigned dose. This later re-randomization created a different question from the original comparison: it concerned withdrawal versus continued dosing among participants meeting the response condition, rather than initial assignment to active treatment versus placebo.

The registry describes double masking but does not report further details about who was masked or how masking was maintained. The planned allocation ratio, eligibility criteria beyond the stated psoriasis severity, and the trial's original sample-size justification are not reported in the registry record. The exact procedures for post-Week 16 response-based treatment are described only in broad terms.

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.

Only the first 6 of 7 groups are shown.

Controlled Period

Reasons for not completing this period:

After Controlled Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent to treat. All patients randomized were included in the analysis according to the assigned treatment groups. Patient is considered a non- responder if the patient has used any pre-specified prohibited medications or discontinued due to lack of efficacy, or an AE of worsening of psoriasis, or had missing data at Week 12.

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 Psoriasis Area-and-severity Index (PASI) 75% Improvement From Baseline at Week 12., measured over Week 12.

The primary endpoint is the number of participants who achieved at least 75% improvement from baseline in PASI at Week 12. PASI combines assessments of redness, scaling, thickness, and the extent of body involvement. The registry describes the score's range as 0, best, to 72, worst. The endpoint therefore converts change in a composite psoriasis severity score into a responder outcome: a participant either meets the stated improvement threshold or does not.

A threshold-based endpoint can be useful because it gives a clinically interpretable count of participants meeting a predefined degree of improvement, rather than only reporting an average score change. It also permits direct comparisons of response frequency between randomized groups. However, a responder count does not show the size of improvement for people who did not meet the threshold, nor how far responders exceeded it. Those distinctions matter when interpreting the outcome: the result addresses the proportion meeting this particular criterion, not every possible change in symptoms or disease severity.

The primary analysis is described as intention-to-treat, with all randomized participants included according to assigned treatment. The record further says a participant was considered a non-responder if they used specified prohibited medications, discontinued because of lack of efficacy, or discontinued due to an adverse event of worsening psoriasis. The remainder of the rule following the final listed condition is not reported in the registry record. The endpoint is assessed at Week 12, before the placebo group’s stated crossover to ustekinumab at Weeks 12 and 16.

7. Results Posted in the Registry

• Ustekinumab 45 mg: 67.1% (171/255) versus 3.1% (8/255) on control; risk difference 63.9 percentage points (95% CI 57.8 to 70.1), risk ratio 21.38 (10.75–42.50); unadjusted two-proportion z-test p = <0.001.
• Ustekinumab 90 mg: 66.4% (170/256) versus 3.1% (8/255) on control; risk difference 63.3 percentage points (95% CI 57.1 to 69.4), risk ratio 21.17 (10.64–42.10); 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.

Number of Participants Who Achieved a Physician Global Assessment (PGA) Score of Cleared (0) or Minimal (1) at Week 12

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ustekinumab 45 mg: 59.2% (151/255) versus 3.9% (10/255) on control; risk difference 55.3 percentage points (95% CI 48.8 to 61.8), risk ratio 15.10 (8.16–27.96); unadjusted two-proportion z-test p = <0.001.
  • Ustekinumab 90 mg: 60.9% (156/256) versus 3.9% (10/255) on control; risk difference 57.0 percentage points (95% CI 50.6 to 63.4), risk ratio 15.54 (8.40–28.75); 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 Ustekinumab 45 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Ustekinumab 90 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Psoriasis Area and Severity Index (PASI) 75 Responders at Week 52

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Group 2: Ustekinumab 45 mg Every 12 Weeks: 87.0% (67/77) versus 64.4% (47/73) on control; risk difference 22.6 percentage points (95% CI 9.3 to 35.9), risk ratio 1.35 (1.12–1.64); unadjusted two-proportion z-test p = 0.001.
  • Group 3: Ustekinumab 90 mg Withdrawal: 61.6% (53/86) versus 64.4% (47/73) on control; risk difference -2.8 percentage points (95% CI -17.8 to 12.3), risk ratio 0.96 (0.75–1.22); unadjusted two-proportion z-test p = 0.720.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Group 2: Ustekinumab 45 mg Every 12 Weeks than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Group 3: Ustekinumab 90 mg Withdrawal and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add different kinds of context to the primary PASI 75 result. At Week 12, the Physician Global Assessment outcome broadly follows the primary pattern: the reported responder counts are higher in each ustekinumab group than in placebo, and the sponsor’s reported comparisons have p < 0.001. This is a separate measure of physician-rated status, not a replication of the PASI scale. The Week 52 outcome addresses later PASI 75 response after response-guided treatment and re-randomization, so it relates to maintenance and withdrawal rather than the initial placebo-controlled question.

The registry lists change from baseline in Dermatology Life Quality Index at Week 12 as a secondary outcome, but its result is not reported in the registry record. The set of posted secondary results is therefore incomplete relative to the outcomes listed. The available secondary results should not be used to imply a complete assessment of every planned outcome or every dimension of patient experience.

Secondary findings are generally less definitive than the primary result when many outcomes, time points, doses, or subgroup comparisons are examined. Unless the analysis plan specifies how to control the overall chance of false-positive findings, repeated testing can make nominal p-values appear more persuasive than they are. Multiplicity procedures are not reported in the registry record. This does not make secondary findings irrelevant; it means their role is supportive and their uncertainty should be considered alongside the primary endpoint, study design, and whether each analysis was prespecified.

The Week 52 comparisons have a further interpretive limitation: treatment allocation in that phase followed response at Week 28 and Week 40, and eligible participants were re-randomized to withdrawal or continued maintenance. These comparisons concern the population that met those response conditions. They should not be combined conceptually with the original randomized groups as if all participants had remained on their initial treatment throughout. The secondary outcomes suggest a broader set of questions, but they do not change the definition or result of the primary Week 12 endpoint.

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

• Number of Participants Who Achieved a Physician Global Assessment (PGA) Score of Cleared (0) or Minimal (1) at Week 12
• Change From Baseline in Dermatology Life Quality Index (DLQI) at Week 12
• Psoriasis Area and Severity Index (PASI) 75 Responders at Week 52

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant is classified as achieving PASI 75 or not achieving it at Week 12. The registry posts numbers of responders and group sizes, so the natural descriptive summary is the response frequency in each treatment group. A comparison can then be expressed as an absolute risk difference, which is the response probability in one group minus the response probability in the comparator. The recalculated values use the posted counts and are simple, unadjusted comparisons.

What does the risk difference tell us?

The risk difference describes how far apart the two groups are on an absolute probability scale. A positive value for an active-treatment-versus-placebo comparison indicates a higher observed response probability in the active group. Its confidence interval expresses uncertainty about that absolute contrast. If the interval includes zero, the data are compatible with no difference under the model used; if it lies entirely on one side of zero, the range of compatible estimates excludes zero at the stated confidence level. These are general interpretations of confidence intervals, not a substitute for clinical judgment.

Other measures can express the same binary comparison on different scales. A risk ratio compares response probabilities as a ratio; an odds ratio compares odds. These scales can look numerically different and answer different descriptive questions, so the scale should be named rather than treating all effect estimates as interchangeable. The registry’s reported tests are CMH chi-square analyses, while the simple re-calculations are unadjusted risk-difference comparisons. The method used for the sponsor analysis and the method used for the re-calculation are therefore not identical.

Why is the reported test different from the re-calculation?

The registry reports a Cochran-Mantel-Haenszel (CMH) chi-square test for each primary comparison. In general, CMH methods can compare groups while accounting for strata. The registry record does not describe the strata, the details of the model implementation, or any covariate adjustment. Consequently, the reported p-values can be cited, but the precise analysis structure cannot be reconstructed from the available record. The re-calculated results use only the posted group counts and do not claim to reproduce any adjustment or stratification used by the sponsor.

A p-value assesses how inconsistent the data are with a specified null hypothesis under the test’s assumptions. It does not give the probability that the null hypothesis is true, the probability that the finding is due to chance, or the magnitude of the treatment difference. The posted p-values, p < 0.001, indicate that the reported tests found strong evidence against their null comparisons, but interpretation still depends on the endpoint, analysis population, design, and multiplicity context.

What does the intention-to-treat description mean?

The primary population is described as intention-to-treat: all randomized participants were analyzed according to assigned group. This preserves the comparison defined by random assignment, even if participants later discontinue or receive other treatment, subject to the endpoint’s specified non-responder rules. The record states that prohibited medication use, discontinuation for lack of efficacy, and discontinuation because of an adverse event of worsening psoriasis led to non-responder classification. The record excerpt does not provide the rest of that rule, or further details about missing endpoint measurements and their handling.

General statistical principle: how missing outcomes are treated can affect a binary response estimate, especially if missingness differs across groups or is related to response. Counting particular discontinuations as non-response is one explicit outcome rule; it does not reveal the handling of every possible missing-data circumstance. Further assumptions or sensitivity analyses should not be inferred when they are not described in the registry record.

Why does the later outcome need separate interpretation?

The Week 52 PASI 75 outcome follows response-dependent treatment and re-randomization at Week 40 among participants meeting the specified PASI 75 condition at both Week 28 and Week 40. It is therefore not the same estimand as the initial randomized comparison at Week 12. Comparisons between withdrawal and maintenance groups address treatment continuation in the qualifying re-randomized population. They do not provide an unselected comparison of the original randomized groups across the full follow-up period.

General statistical principle: randomization helps balance prognostic factors between assigned groups at the point of assignment. When later analyses include only participants meeting a response condition, the analyzed groups are selected by post-randomization experience. The resulting analysis can still answer its defined question, but it should be interpreted in that selected population and treatment context. A later re-randomization can support a separate randomized comparison among those eligible, but it does not undo the selection involved in reaching eligibility.

These methods explain why the endpoint definition, analysis population, treatment timing, and comparison all matter alongside a test result. Statistical significance alone cannot tell whether an outcome is comprehensive, whether results persist after treatment changes, or whether the finding generalizes beyond the study population. The registry’s detailed original statistical plan, including its planned adjustment strategy, is not reported in the registry record.

11. Confidence Intervals and Precision

The primary Week 12 re-calculations include 95% confidence intervals for the risk difference between each ustekinumab group and placebo. Both intervals are on the positive side of no difference, consistent with the direction of the observed responder counts. Their widths indicate uncertainty remains about the exact size of the difference; the interval is not a guarantee that the true value lies within its endpoints. It describes a range generated by the stated statistical procedure and its assumptions.

Precision is distinct from statistical significance. A small p-value indicates that the observed data are difficult to reconcile with a no-difference hypothesis under the test assumptions. The confidence interval adds information about the range and scale of effects compatible with the data. A result can be statistically clear while the precise magnitude remains uncertain. The re-calculated intervals are unadjusted and should not be mistaken for intervals from the sponsor’s CMH analysis, for which the registry does not report an effect estimate or confidence interval.

The Week 12 groups have similar reported sizes, and the primary outcome has a large contrast in responder counts between placebo and each active-treatment group. Those data provide more information about the initial comparison than the later selected re-randomized groups provide about withdrawal and maintenance. The Week 52 estimates involve smaller groups and, for some comparisons, intervals that span both negative and positive differences. Such intervals indicate that the observed data do not precisely locate the contrast relative to no difference.

Confidence intervals do not address every source of uncertainty. They do not account automatically for multiplicity, missing-data assumptions, outcome measurement issues, or limitations in generalizability. Nor do they establish clinical importance. The registry record does not report confidence intervals for the sponsor’s CMH tests, so the uncertainty intervals discussed for the primary risk differences belong to the unadjusted re-calculations only.

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 figures are planning illustrations based on the observed effects, not reconstructions of the trial’s original design. For these binary outcomes, the figures represent participants per arm, not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect to detect equal to the listed fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrated number of participants per arm for a design that would have 80% power under those assumptions and for the specified effect size. The 90% power column gives the corresponding planning number for 90% power. Power is the probability, under the assumed effect and statistical model, of rejecting the null hypothesis when that assumed effect is true. These are hypothetical planning calculations, not a description of the analysis performed in this trial.

The rows use the full observed effect, 75% of the observed effect, and 50% of the observed effect. As the assumed effect becomes smaller, more participants are required to distinguish it from no difference with the same planned power and significance level. For example, the primary comparison’s illustration for 100% of the observed effect gives 8 participants per arm for 80% power and 10 for 90% power; planning for 50% of the observed effect gives 23 and 30, respectively, for the 45 mg comparison. Those figures are sensitive to the strong observed contrast and should not be treated as a general target for a future study.

This is not observed power. It does not measure the probability that the completed trial detected an effect, and it cannot replace confidence intervals or the reported analyses. The illustrations use the observed effect as a planning input, which can make estimates especially optimistic when the observed difference is large. A real design would need prespecified assumptions about the target effect, outcome frequency, allocation, analysis, and other design considerations; those original decisions are not reported in the registry record.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.031; treatment proportion p₁ = 0.671; average p̄ = 0.351.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6750 = 1.3229.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5013 = 0.4219.
4. n = (1.3229 + 0.4219)² / (0.6392)² = 7.5, rounded up to 8 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 <- 0.0313725490196078                          # control proportion
p1 <- 0.670588235294118                          # 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(267969)
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 = 8 (80% power), 10 (90% power)
 75% of observed effect: n per arm = 13 (80% power), 16 (90% power)
 50% of observed effect: n per arm = 23 (80% power), 30 (90% power)
power.prop.test: 7.5 
Simulated power at n = 8 per arm: 0.872 (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 analyses use a Cochran-Mantel-Haenszel chi-square test for placebo versus ustekinumab 90 mg and for placebo versus ustekinumab 45 mg. Each is reported with p < 0.001. The record does not report a sponsor effect estimate or confidence interval for these analyses. The simple re-calculations instead use the posted responder counts to estimate unadjusted risk differences and confidence intervals, and their p-values are also reported as p < 0.001.

These analyses agree in the direction and broad statistical conclusion: each active group has more Week 12 PASI 75 responders than placebo, and both reported sponsor tests and unadjusted re-calculations indicate evidence against no difference. They are not identical analyses. CMH may account for strata, but the registry record does not identify the strata or provide enough detail to reproduce the sponsor’s procedure. The re-calculation is an unadjusted comparison of summary counts and should be read as a transparent descriptive check, not as a replacement for the sponsor analysis.

There is no discrepancy flagged between the posted results and the re-calculation. In general, if a discrepancy is identified, the sponsor’s own analysis takes precedence for the trial’s reported inferential result. The re-calculated estimates remain useful for explaining absolute differences and their uncertainty, while their limitations should remain explicit. Neither set of p-values alone establishes the clinical importance, durability, or generalizability of the Week 12 finding.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports one primary outcome and several secondary outcomes, with analyses involving more than one dose and more than one time point. The primary sponsor comparisons are reported separately for each ustekinumab dose versus placebo. The record does not report whether the trial used a multiplicity adjustment, a hierarchical testing strategy, or another procedure to control the family-wise false-positive rate across outcomes and comparisons. The original statistical analysis plan is not reported in the registry record.

Multiplicity matters because, in general, carrying out many statistical tests increases the chance that at least one result appears statistically significant even when the corresponding null hypotheses are true. This is a general statistical consideration, not a claim that any particular finding in this trial is false. The p-values should therefore be interpreted in light of the distinction between the primary comparison and secondary or later analyses. The primary outcome has a clearer confirmatory role than the wider collection of secondary findings, while the missing multiplicity details limit assessment of the overall testing strategy.

The primary outcome population is described as intention-to-treat, with all randomized participants analyzed according to assigned groups. The record also specifies that participants using prohibited medications or discontinuing for lack of efficacy or an adverse event of worsening psoriasis were considered non-responders. The rest of the stated rule is incomplete in the registry record, and further details on missing measurements, withdrawals for other reasons, and sensitivity analyses are not reported in the registry record.

Missing-data handling is important because a responder endpoint requires a classification for participants whose Week 12 status is unavailable. General statistical principle: conclusions can depend on whether missing outcomes are treated as non-response, excluded, imputed, or handled through another model, particularly if missingness is associated with treatment or outcome. The specified non-responder conditions clarify part of the rule but do not establish how all missing data were handled.

Further analysis details, including the planned strata for the CMH tests, the treatment of protocol deviations, and the full statistical analysis plan, are not reported in the registry record. No unreported procedure should be assumed.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

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: coronary artery disease (2.5%), myocardial infarction (1.7%), atrial fibrillation (1.6%), appendicitis perforated (1.6%), angina unstable (1.2%).

The registry posts serious adverse-event counts for the controlled period and for periods after the controlled period. During the controlled period, serious adverse events were reported for 2 participants in the placebo group, 2 in the ustekinumab 45 mg group, and 4 in the ustekinumab 90 mg group. The corresponding counts for other adverse events were 81, 102, and 84. These are counts among the stated at-risk group sizes, not adjusted comparisons of event risk.

After the controlled period, the posted serious-event counts were 20 for placebo participants who crossed over to 45 mg, 18 for those who crossed over to 90 mg, 38 in the 45 mg group, and 33 in the 90 mg group. The corresponding other-adverse-event counts were 110, 102, 207, and 207. These later groups have different treatment histories and follow-up contexts from the initial controlled-period groups, so the counts should not be compared as though they came from one concurrent randomized comparison.

The registry lists several serious-event terms with percentages, including coronary artery disease at 2.5%, myocardial infarction at 1.7%, atrial fibrillation and perforated appendicitis at 1.6% each, and unstable angina and osteoarthritis at 1.2% each. The denominator and detailed event-level context for these listed percentages are not reported in the registry record. Death counts are not reported in the registry record. Counts alone do not establish whether events were caused by treatment, and these figures do not provide a complete benefit-harm assessment.

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

The Week 12 results show that more participants in each ustekinumab group than in the placebo group were recorded as achieving PASI 75. Both sponsor-reported comparisons have p < 0.001, and the unadjusted risk-difference re-calculations point in the same direction. The confidence intervals for those re-calculations convey uncertainty around the size of the absolute differences. This is evidence about a defined response threshold at a defined time in the trial population.

That finding does not mean every participant responded, or that the same response would occur for every person with psoriasis. It does not describe how much participants improved if they fell short of PASI 75, whether response continued, or what happened to quality of life. Although the registry lists a Week 12 DLQI outcome, its result is not reported in the registry record. The primary endpoint also does not measure every aspect of psoriasis or every possible adverse effect.

The Week 12 contrast is embedded in a treatment sequence: the placebo group crossed over at Weeks 12 and 16, treatment after Week 16 depended on response, and some participants meeting the Week 28 and Week 40 response condition were later re-randomized to withdrawal or maintenance. Thus later results answer different questions from the initial randomized comparison. They cannot be read as an uninterrupted placebo-controlled comparison through Week 52.

The results do not, on their own, establish that one dose is better than the other. Each reported primary sponsor test compares a dose with placebo; a direct dose-versus-dose primary analysis is not reported in the registry record. The findings also do not establish effects in populations or care settings not represented by the trial, or determine the net clinical value of treatment. Such judgments require broader evidence and clinical context. The statistical results describe the recorded endpoints and analyses; they are not medical advice or a guarantee of an individual outcome.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through the endpoint definition, assignment process, analysis population, and treatment timeline rather than through a p-value alone. PASI 75 is a thresholded response outcome derived from a composite severity score. Reporting responder counts makes the primary question interpretable as how many participants met a specified improvement criterion, while the risk difference translates the comparison into an absolute scale.

The trial also shows how a placebo-controlled comparison can have a bounded time window. Placebo crossover began at Weeks 12 and 16, and later treatment depended on clinical response. Consequently, the Week 12 comparison and the later withdrawal-versus-maintenance question are distinct estimands. Recognizing that distinction prevents later selected-group results from being interpreted as if they preserved the original three-group comparison.

Another statistical lesson is that reported sponsor tests and simple re-calculations may use different methods. The sponsor reports CMH chi-square tests, while the re-calculations use posted summary counts for unadjusted risk differences. Their agreement in direction is informative, but the re-calculation cannot recover unreported stratification or replace the sponsor’s analysis. Confidence intervals complement tests by showing the uncertainty around an estimated effect.

Finally, the registry’s missing information is consequential: the original sample-size justification, detailed statistical plan, multiplicity procedures, some missing-data details, and the DLQI result are not reported in the registry record. Clear limits on what can be inferred are part of sound statistical interpretation. The record supports a focused reading of the Week 12 response comparison, while leaving important questions for outcomes, safety context, and analysis choices unresolved.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the original sample-size justification, the planned allocation ratio, or the full statistical analysis plan. It also does not explain the strata used for the sponsor’s CMH tests or give sponsor effect estimates and confidence intervals. As a result, the sponsor analyses cannot be fully reconstructed from the posted summary. The unadjusted recalculations provide a separate description, but they do not replace the trial’s own analysis.

The outcome description includes a truncated non-responder rule. It identifies prohibited medication use, discontinuation for lack of efficacy, and discontinuation due to an adverse event of worsening psoriasis, but the remainder is not reported in the registry record. The handling of all other missing Week 12 measurements, protocol deviations, and sensitivity analyses is also not reported. These omissions limit evaluation of how robust the primary responder classification is to alternative assumptions.

The registry lists change from baseline in DLQI at Week 12, but its result is not reported in the registry record. Multiplicity procedures are not reported, despite multiple outcomes, doses, and time points. The posted results therefore do not allow a full assessment of the planned testing hierarchy or the overall error-rate strategy.

Later outcomes have additional design constraints. Week 52 response is reported after treatment depended on clinical response and eligible participants were re-randomized at Week 40. Those results apply to the selected re-randomized population, not all participants in the original allocation. The record gives counts, but further detail about follow-up, exposure, and event-level safety context is not reported. Generalizability beyond the study population and treatment schedule cannot be determined from these registry summaries alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Safety and Effectiveness of Ustekinumab (CNTO 1275) in Patients With Moderate to Severe Plaque-type Psoriasis — NCT00267969.
• Registry record last updated 2013-06-17; status last verified 2013-06.
• Results first posted 2012-08-24.
• 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

NCT00267969 is a completed phase 3, randomized, double-blind, parallel-group, placebo-controlled trial of ustekinumab for moderate to severe plaque-type psoriasis. Enrollment was 766. The primary endpoint was PASI 75 response at Week 12, analyzed by assigned treatment group in an intention-to-treat population. The sponsor reported CMH chi-square comparisons of both ustekinumab doses against placebo, with p < 0.001 for each.

At Week 12, the posted responder counts were 8 for placebo, 171 for ustekinumab 45 mg, and 170 for ustekinumab 90 mg. The unadjusted recalculations agree in direction with the sponsor-reported analyses. Placebo crossed over to ustekinumab at Weeks 12 and 16; later treatment depended on response, and eligible participants were re-randomized at Week 40 to withdrawal or maintenance. These design features make later results distinct from the primary comparison. Details of the original statistical plan, multiplicity procedures, and some missing-data handling are not reported in the registry record.